"Don't Work on Things That Don't Work"
At the time of this writing Kim Huard was one of Genentech’s Senior Scientists, and has spent a decade looking for new medicines. She spent eight years at Pfizer at the Groton and Cambridge sites before joining us in California. She's currently a Director in the Discovery Chemistry department leading teams of scientists in pursuit of new drugs.
When Dennis interviewed at Genentech, he asked her for one piece of advice on how to succeed in drug discovery. "Don't work on things that don't work!" — she laughed. Recently Dennis got to ask Kim more about where this gem came from and what it really means for drug hunters.
"Maybe the key question is, “will inhibiting the target lead to the desired therapeutic effect?” and after testing the idea with high quality tool compounds in a relevant disease model, the answer is clear. Often times, it’s not that straightforward."
DH: Where did you first hear “don’t work on things that don’t work?”
KH: I first heard it from one of my previous supervisors at Pfizer almost 10 years ago. It was early in my career and wasn’t clear to me what he meant. Of course, no one wants to spend years working on a project that is going nowhere but how do you know?
DH: What does it mean to you today?
KH: For me, it means to first make sure the long-term goals of a project are as clear as possible, and then identify the key questions or missing information related to those goals. What could cause this project to be unsuccessful?
Each unanswered question carries some level of risk for the project. Some questions can be addressed with an easy in vitro experiment while others require an expensive clinical study to obtain conclusive answers. So, it’s important to be able to recognize early on what the key questions are, what risks are associated with them and how fast can they be answered. Part of our job is to think of creative ways to get these answers quickly and efficiently.
As more data is generated, the key questions for a given project may change so clarifying project goals and thinking about key questions routinely can help teams adjust, focus and not get distracted by the many things that can keep us busy.
"The more people you get thinking about key questions, ... the less likely we are to end up spending a long time working on something that doesn’t work."
DH: Who should be involved in figuring out what the key questions are for a project?
KH: Choosing the right questions to focus on is key for the whole project team. In my experience at Pfizer and now at Genentech, project teams are fully integrated such that a chemistry lead can be involved in the biology, safety, and DMPK discussions, and vice versa. This makes it easier for every functional lead to think about whether their team’s strategy aligns with what the project really needs, and to react quickly when project needs change.
More broadly, I think this is where bringing the drug discovery community together is important. We all get burned by different things on various projects and can use it to build collective experience. These different experiences help people come up with different ideas and approaches to solve problems. This is part of what makes our work so interesting. The more people you get thinking about key questions, the richer that list of known questions (and ways to answer them), and the less likely we are to end up spending a long time working on something that doesn’t work.
DH: What do programs that “don’t work” look like?
KH: Sometimes programs come to a “clean,” data-driven stop decision. Maybe the key question is, “will inhibiting the target lead to the desired therapeutic effect?” and after testing the idea with high quality tool compounds in a relevant disease model, the answer is clear.
Often times, it’s not that straightforward. For one program I worked on, genetic inhibition of target expression was beneficial for the disease of interest in rodent models, which was promising. The project team identified a few key questions and initiated work to answer them in parallel.
In order to evaluate if the attractive phenotype observed in genetic models could be reproduced using small molecules, we developed tool compounds that achieved good exposure in rodents. However, their absorption, distribution and elimination turned out to be predominantly driven by transporters. Since the transporters involved were not well characterized, we couldn’t be confident in human pharmacokinetics predictions for these molecules.
From the beginning of the project, we also questioned the relevance of the rodent models to human disease and when we looked at target expression across species in parallel with our chemistry optimization efforts, we discovered rodents were quite different from humans, making it unclear how applicable rodent models were.
In the end, with the small molecule inhibitors we were able to demonstrate efficacy in a rodent model. But since we had only modest confidence in the translatability of efficacy from rodents to humans and had low confidence in our human dose projections for this chemical series, we recommended deprioritizing the project and focusing on more promising programs in the portfolio.
"Unfortunately, there’s no crystal ball to predict what will or won’t work before doing the hard work of asking and answering the right questions. But by making sure we stay focused on answering the important questions as a team, we can get through those key decision points faster to work on new things that might work."
DH: Just because something doesn’t work today doesn't mean that same project won't work 30 years from now, right?
KH: Agreed! Sometimes modulation of a target doesn’t lead to the desired effect, because of a redundant function or compensatory mechanism for example. In such cases, learning more about the biological pathways may help identify a better angle to modulate them. Functional inhibition of proteins with a scaffolding role may not provide the desired phenotype, but their proteosomal degradation might.
In that regard, new modalities that are now available also represent a good opportunity to revisit things that didn’t work before. Technological advancements, new assays and new models allow us to optimize compounds in ways that were difficult to before. The new data generated can also change the way we think about the original questions, leading us to ask better questions and find new ways to answer them.
Which brings us back to the earlier point about the importance of community – the investments from various organizations in building and sharing fundamental understanding of biology, newly developed modalities, new assays and new models, are so important. By changing the way we think about aspects of our work, these shared investments can result in new solutions for old problems.
"Projects with a lot of unanswered questions are the projects that create many opportunities to work closely with people from other departments and backgrounds to find creative solutions and to learn a lot along the way."
DH: What would you say to scientists who may be facing a failing project for the first time?
KH: Even if the team is already asking the right questions, projects have various layers of complexity and it takes time and a lot of work to answer those difficult questions. And it’s inevitable that some projects just won't work. Unfortunately, there’s no crystal ball to predict what will or won’t work before doing the hard work of asking and answering the right questions. But by making sure we stay focused on answering the important questions as a team, we can get through those key decision points faster to work on new things that might work.
Finally, walking in now with eyes wide open, we shouldn’t be afraid of challenging projects. Projects with a lot of unanswered questions are the projects that create many opportunities to work closely with people from other departments and backgrounds to find creative solutions and to learn a lot along the way.
Edited and condensed from two conversations.
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