Time and attention
Summary: Our time and attention are limited resources. Rather than distribute them willy-nilly, it is better to intentionally focus on projects that give us joy, about which other people are excited, and that we are best qualified to do. And that are important and awesome.
"Really successful people say no to almost everything." - Warren Buffett (supposedly)
Every so often I have the same epiphany: I will never accomplish everything I want to. (True in life, too, but here I'm talking about research.) Of course, this makes perfect sense given that we only have so many hours in a day. But emotionally it never really sinks in—I have so many projects I want to do, and can't bear the thought of "giving up" on any. What's a scientist to do?
One approach—and quite honestly the one that I've taken most often—is to not give up on any projects, but to juggle as many as I can. Of course some get done, and others don't, so effectively I have indeed given up on several lower priority ideas. But I haven't admitted it. So I feel like I've won some sort of internal moral victory. (And part of me still expects that someday, magically, all of these projects will still get done.)
A second (and probably better) approach is to limit myself in what I plan to accomplish. This intentionality encourages me to use my time strategically, leading to a more sane self and probably better science.
These points are both important. Although I want to be an excellent scientist, I'd also like to have time for family, friends, exercise, and the necessary everyday tasks of home repair, doing laundry, vacuuming, etc. These things all too easily fall by the wayside unless I make a conscious effort to limit the time I put into work. So, focusing my work may help me to do a better job of accomplishing the various things I'd like to do in life.
At the same time, reducing the time spent on work makes me worry about lost productivity, and so potentially improving my science is an important part of this discussion. For me, one motivating factor in the never-ending science treadmill is job security (such as it is): papers and grant submissions feel like one part of my career that I actually have control over. Focusing my research means turning down some opportunities to work on others; this is scary because I am always worried that I'll pick the "wrong" project to focus on. However, by realizing that I may actually do better science if I am more intentional about how I spend my time and attention, I am more likely to follow through. Regardless of the number of hours I spend on research, being spread too thin intellectually is tiring and can limit scientific progress.
Having committed to become more focused in my science, the obvious question is: what projects do I work on? I've decided that a good place to start is the intersection of the following:
- Projects that give me joy
- Projects other people are excited about
- Projects that my lab can do really well
- Projects that are important and awesome
Projects that give me joy
I almost wrote that of course all of the projects clamoring for my attention are things that give me joy. But actually, this isn't true. For example, a project may have come about because I'm interested in a collaboration (the people) but not necessarily the scientific content; others are publishable or fundable (see below) but are not intellectually engaging. Although some of these projects may be worth pursuing, as much as possible I'm trying to spend my time pursuing topics which are intellectually engaging and exciting.
The first draft I wrote used the phrase "interested in"—as in, "I should only work on things I'm interested in". How bland. There are a lot of topics in the world which could be interesting—this is a horrible metric (and probably why I currently have 75+ "active" research projects in Omnifocus). So I opted to borrow a principle from Marie Kondo’s advice about possessions: only keep things which give me joy.
The picture gets complicated by the fact that different aspects of projects can be joy-giving. The most obvious example is that I have several wonderful collaborators, and having an excuse to work with colleagues on a shared project is one of my favorite things about being a scientist. So, there are projects for which the scientific content is not the main driving factor in determining their "joy" level.
Of course, every project will have aspects that are not joyful. I don’t think I will ever feel joy when working on an IRB protocol. However, when I go through my list of research projects, it's surprisingly easy to sort them into those that I’m excited about and those that I feel like I "should" do for whatever reason. I’m trying to move to a place where more items on the list go in the “joy” category.
If my own joy were the only metric, this might be easier, but it’s not. If no one else cares about what I’m doing I won’t last long as a researcher.
Projects other people are excited about
Over the past couple of years I've changed the way I've internally defined what other people "being excited about my research" means. Initially it meant “this research could get published"; then "this research is fundable". Both of those are still important, but not the whole story (although it's too easy to start thinking this way).
Here, too, my first draft talked about projects in which other people were "interested". You don't want your grant reviewers to merely be “interested” in the research you propose; you want them excited. So, I’ve been trying to use the right words when talking to myself—doing so makes a huge difference.
Of course, this is not to say that research that can get published and funded is not important. In theory it would be great if projects met all of these criteria—fundable, publishable, and overall excitement—simultaneously. However this isn't always the case: a new idea may be high on the excitement factor, but if it's brand new and doesn't have a lot of preliminary data it may not be easy to get it funded. So there is typically a trade off between risk and possible reward.
A way that I've taken to dealing with this tension between risk and reward is to think of research projects like any investment portfolio, and aim for diversification. I try to have some ideas in each of these categories: likely to be published, possible to be funded, and some chance of being totally awesome.
Projects my lab is uniquely qualified to do (or at least, that we can do really well)
There are many cognitive neuroscience labs, many experimental psychology labs, and many audiologists studying speech processing. What is our lab’s contribution to this field? Is there a technique or theoretical framework that we can bring that is unique?
From one perspective, this constraint comes naturally to most of us, in that we are (hopefully) not going to regularly embark on projects that we have no idea how to accomplish. However, within the realm of things that "our lab can do" lie a range of topics, some of which we may be better qualified at than others. Or, perhaps looking 5 years into the future we can develop a technique or combination of approaches that fills an important niche. The point is to move beyond the easy limitation of "what can we do" towards being intentional about what we may be uniquely qualified to do.
Focusing on our strengths is practical, but also a responsible use of our funding. And, hopefully, an efficient way to promote scientific discovery.
Projects that are important and awesome
Hopefully the research projects that give me joy, that other people are excited about, and that we do well, are also important and awesome. Maybe this is my personality, but I often find I don't push myself scientifically if I focus on things that are "publishable", "fundable", or "interesting". I have to explicitly remind myself to do awesome work or I may not get around to it (too much mundane work seems more urgent).
(Yes, I have some gimmicks to help—for example, I have a post-it note on my computer that reminds me to "keep everything awesome". I sometimes make extra notes of this when writing grants and planning projects.)
Don't let the brevity of this section fool you. Awesomeness is one of the most important, but rarest, qualities of scientific research, and it seldom happens without a strong dose of intentionality.
Where to start: Serial focus
A final point is that it may make sense to start with the most important (or the most difficult) area. For example, I tend to go from the top of the list and start with projects that give me joy, weeding out projects that don't meet the other criteria. However, I sometimes find this criterion too permissive, and it could be that a better order would be to start by limiting myself to projects that are important and awesome, and then only pick up ones that give me joy. The idea is to develop a decision system that is actually useable, and helps to focus my attention the best way possible (i.e., helps me to say no to a lot of things). If you find that everything gives you joy, this is probably not a great criterion to use to help focus your efforts.
Optimizing our time and attention is always difficult, especially in situations in which there are multiple, not-always-congruent dimensions. It's probably not realistic to think that every single project I spend time on will fit all of these criteria, but they have been helpful to me in prioritizing my research efforts and coming up with new projects.