Research ideas, part 3: Ask questions

I’m fascinated by the television show Shark Tank, where professional investors listen to a brief pitch from aspiring entrepreneurs, ask a few questions, then make a decision on the spot to invest (or not invest) up to millions of dollars in an idea. Similarly, if you’ve ever pitched project ideas to someone who has been doing research for a significant amount of time, they can often tell you very quickly whether they think your idea has promise.  It may seem as if these people are “going with their gut” as they make decisions, but I can almost guarantee that this is not the case, and that each decision is the result of a systematic and calculated evaluation process. These individuals have just practiced it enough that it becomes almost instantaneous.

You might be tempted to think that if you’re not giving away millions of dollars on Shark Tank, then you don’t need this ability to quickly judge the merit of ideas.  Not so.  As we discussed previously, if you are in or aspiring to a research career, you need ideas, and to have good ideas, you need to have a lot of ideas.  This means that you need to be able to quickly evaluate each idea and decide if it is worth the investment of your time to develop further.  There are many ways to do this – our process involves a series of questions:

• Has this exact thing already been done? This may seem obvious, but it’s surprising how tempting it can be to put off asking this, as it is the one question that can completely kill an idea.
• Is there a real problem or question here? Is there something that we don’t know or can’t do? Is that thing potentially impactful?
• Have others worked toward solving this problem or answering this question? This is a subtler version of the first question – maybe nobody has done exactly what you are thinking of doing, but likely someone has reported a technology to help meet the need or data toward an answer to the research question. If the answer to this is “yes,” then ask whether there are still limitations to the reported approaches or knowledge that is missing. Will your idea help overcome that?
• Is this really the best way to solve the problem or answer the question? This can be a tough question to answer honestly, as we often become so enamored with our approach that we don’t want information that would compel us to let go of the idea. A productive way to push through that discomfort is to ask: If there is a better way, what is it? Has that already been done? Would I be excited to work on the “better” idea?
• Is this feasible? It may seem odd that this question is coming so late in the game, but that is intentional. If you realize at this point that there is a feasibility challenge, it is likely that you can find a creative solution to reduce risk, then keep going.  However, if you spend significant time up front convincing yourself of feasibility only to later realize that the idea is not significant or impactful, that’s not an ideal situation.

When you’re starting out with generating research ideas, it may take quite a bit of time to think through these questions. The good news is that as you practice and gain experience, you will become much more efficient, and likely gain the ability to triage most ideas within seconds of generating them.

The questions above are aimed at deciding whether an idea has enough merit to warrant a plan. If you’ve gotten this far and haven’t killed the idea yet, it’s time to start asking some more practical questions: 

• What is most likely to go wrong? This question is in line with the “fail fast” philosophy – if something isn’t going to work out, that’s fine, but you want to find out sooner rather than later. As logical as that sounds, it can be tough to act on. Again, it’s important to push through the discomfort, figure out what is most likely to cause a complete failure of the project, and develop a strategy to run at that answer.
• If things do go wrong, what are the alternative approaches? Pretty self-explanatory, but it’s never too early to start thinking about this!
• If nothing works, what can I still learn or produce? While you obviously hope not to end up in this situation, sometimes that’s just where research takes you, even with a really good project idea.  It’s important to think ahead about whether you could “turn lemons into lemonade.” If the answer is that nothing can be learned or produced if things don’t work, the project might still be worth trying, but at least acknowledge that risk up front, and set a timeline for how long you’re willing to commit before you succeed or drop the project. 

If my group and I can make it through this entire series of questions and still have a high level of enthusiasm for an idea, then we recognize it’s something we should give serious consideration to, and we already have the start of a strategic plan to get going!  Stay tuned for next month, where I’ll close out this series with some practical tips for what to do with the ideas that successfully make it through this mental gauntlet.

Think of a key question that I missed? Use a totally different process? Share that in the comments!