How do you prioritize research?
Posted: August 28, 2012 | Author: Hilary Mason | Filed under: blog | 9 Comments »
One of the most fun and challenging parts of my job is setting bitly’s research agenda. We’re a startup, so this means prioritizing the set of questions we look into in the context of what will be most beneficial for the rest of the business, for the short and long-term, by creating opportunity and opening up potential futures. We work on a wide variety of projects, from pure research to press collaborations to infrastructure and experimental products.
We always have a list of research questions way longer than we have time and resources to pursue, so we developed a process for evaluating whether a given question is worth pursuing at a particular time.
This is the kind of process that I’ve only discussed with several people over whisky (thanks!), but not seen written up. I initially had a much longer list of questions but have decided to keep it as simple as possible, to frame a discussion but not dictate or burden it. I hope it’s helpful and I would love to hear about other appproaches.
For each research question that we might look into, we ask the following:
- State the research question.
- How do we know when we’ve won?
- Assume we’ve solved this question perfectly. What are the first things that we’ll build with it?
- If everyone in the world uses this, how does it change human behavior?
- What’s the most evil thing that can be done with this?
State the research question.
It’s important to state the question in language that everyone can understand. The bitly team comes from a variety of scientific and business backgrounds, and we’ve developed some of our own common vocabulary, but it still takes a bit of effort to make sure that everyone understand the fundamental challenge and why it’s interesting.
How do we know when we’ve won?
Here we define the metrics that we’ll use to measure our success. For some questions, this is obvious, and for others it’s impossible to define — we can at least acknowledge that ahead of time.
Assume we’ve solved this question perfectly. What are the first things that we’ll build with it?
This question allow us to assess the potential business and product impact. What capabilities will we have with this that we don’t have now? It allows us to keep the long-term research vision in mind while still optimizing for shorter-term opportunities.
If everyone in the world uses this, how does it change human behavior?
What’s the maximum potential impact of this work? If it’s not inspiring, is it worth pursuing at all?
What’s the most evil thing that can be done with this?
I don’t ask this question to encourage evil (>:]) but as a creative tool for expanding how we think about validity, impact, and potential applications of the research. The label evil is so ridiculous that it permits people share their craziest ideas. Plus, it’s always a fun conversation to have.
Finally
I’m always revising this list, and I would love to hear how you think about prioritizing your work.
)
