I was having beers with a group of faculty at a recent conference and we were talking about our careers in psychology. We each had quite different takes on our academic lives. One senior researcher, probably the most prominent person in the group, said something that stunned me. “It wasn't until a few years ago — more than 30 years into my career — that I realized there is more to this than just publishing papers and getting grants,” he said. “Maybe we should be producing something useful to society with our research.”

At this time of year, lots of eager scientists are arriving on campuses around the world to take the next step in their research careers. I have seen many of them ask for advice on social media and in other outlets. I've been pondering what I have to say to someone about to begin graduate school. It occurred to me that my advice is directed to senior faculty as much as it is to scholars just starting out: don't be like my drinking buddy. This post describes strategies to make your research useful.

What surprised me about his comment was how late in the game he'd come around to the idea of societal value in research. Here was a person who really cared about having social impact. How had it only now occurred to this scholar that his work could actually address some of the issues he raised as afterthoughts in the implications sections of his papers?

There are many answers, but the biggest culprit, the thing that most directly undermines our best intentions, is ourselves. More precisely, it is our exquisitely fine tuned reward learning systems. As another prominent researcher at the bar put it, “You publish a paper, then you get a grant. So then you write another paper, and get another grant. That's all there is.”

Like the rats in so many of our studies, we, too, are quite capable of learning to hit the feed bar to get a reward pellet. After a while, we learn exactly what kinds of studies, papers, topics, questions, theories, samples, methods, designs, and so forth, will earn us the most reward for the least effort. Plus, the ample rejection ensures that the reinforcement is intermittent and unpredictable - exactly the right conditions to get us hooked. I am ashamed to admit how often I have found myself throughout my career compulsively checking the status of a paper or a grant proposal. Perhaps the astounding thing is that any of us can break away and think about broader priorities within the habitat we've constructed for ourselves.

What's the alternative? I mean, we need to publish papers and get grants to survive. As with addiction, the preferred solution is to avoid getting started in the first place. With that in mind, my first tip is:

Find the right rewards

As my beery colleagues demonstrated, it's all too tempting to hop on to the paper-grant hamster wheel and happily scurry away a career. The system is set up for it. We are set up for it. But you don't want to be facing down emeritus status and asking whether any of it mattered for anything. What would you rather have on your tombstone - something you did that was good and lasting, or your h-index?

Until we reach the utopian future where you can get tenure and promotions without them, you're still going to need publications and grants to survive in this field. So what's the alternative? Remember that those papers and grants are not ends but means. It's always fun to publish a paper, but assume it won't get read by anyone besides the reviewers. The paper itself won't do anything for society. That's up to you. The earlier you are in your career, the easier it will be to reframe the way you think about your job as contributing to solutions to societal problems rather than building your CV.

What are those big problems? What would be a Really Important Issue to work on? Our hamster wheel-myopia can make it difficult to see. For inspiration:

Talk to real people

I used to dread the conversation at Thanksgiving dinner, and I was especially uncomfortable when the topic of my research came up. It felt arduous and tedious to explain all the little theoretical and technical minutiae that motivated my laboratory studies. Eventually, I realized that the problem wasn't my family, but me. Their inability to understand or care about my work was my problem, not theirs. I was choosing to work on topics that researchers but not real people cared about.

Here's a fun game: ask people what they think about when they're alone in a dark room. Responses from academics tend to be about 90% self-presentation, 8% jargon, and 2% content if you're willing to work hard enough to parse their language. In contrast, real people (i.e., non-academics) say things like, “I wonder why I'm in pain all the time,” or “I think about my relationship with family,” or “It feels like we're on the verge of total social collapse and I worry about group-based violence.” Those are all things that science can and does speak to, so why was I spending my precious few days figuring out how 40 year old pictures slightly influenced the ability and willingness of freshmen to push buttons? Really listening to what matters to real people is a great way to get research ideas.

Also, don't forget that journalists are real people. They're actually better than real people for my purposes, because their expertise is in talking to other real people. We scientists often complain about journalists, but we need to take ownership of our contribution to the problem in communicating science to the public through them. We can't expect them to understand our papers and do all the heavy communications work. We need to meet them halfway. So, when a journalist emails you, write back. Work with them. When they ask for input on copy, take it seriously and give it to them. Act like it's your job to bring science to the public, because it is.

There is a strain of thought in academia that cautions against speaking to journalists. My next piece of advice explains why you should reject that strain. 

Don't let the perfect be the enemy of the good

We often wonder if our conclusions are solid or robust enough to responsibly take them to the public at large. “I don't know this to the point of certainty,” this line of thinking goes, “so I shouldn't say anything to a journalist yet. He or she will probably just get it wrong anyway.” That may be true, but consider that alternative for the journalist is simply to write the story anyway without your input. The same holds true for policymakers and other professional groups: they're going to do what they're going to do with or without you. I would rather have a scientist giving input - partial, incomplete and imperfect though it may be - than not. No study will ever be perfect, no conclusion ever certain. The key question to ask yourself is whether there is any bit in there that you are convinced nudges human knowledge in the right direction.

This advise also applies equally well to methodological and statistical hangups. I'm all for using the best available research practices, and these days social media makes it easier than ever to find out what those practices are. Learn them and use them. But also remember that they, like all research practices, are flawed and will shortly be replaced by something better. The inherent imperfection of everything we do is a central feature of science. You don't need to love it, but you do need to make peace with it so you can move on and start disseminating what (limited, flawed) knowledge we can generate with the tools that are available right now.

The notion of making peace with imperfection leads me to my next tip: 

Get out of your own way

This advice was given to me when I stared out as an assistant professor and began recruiting graduate students. A scientist I admire told me, “the best graduate students are the ones who know how to get out of their own way.” Most of us are some variety of perfectionist. We wouldn't have advanced this far in academia, the way the wheel is set up, without being obsessive about getting everything right. In graduate school, this obsession is a serious liability. Your time will be limited more than ever before (and will become even tighter as you move up the pyramid), so spinning your wheels becomes ever more costly. You need to figure out how to be productive in tight time windows.

Getting out of your own way means letting go. Stuck writing the paper because you can't come up with the perfect opening line? Then vomit on the page, write what you can, and trust that it'll come out okay through revision. Obsessing over some new analytic tool that you can't get to work? Finish the project with tools you do know how to use and apply the tool to the next dataset when the software is more developed. Can't find the perfect gif to go with that one slide for your lecture? Do one Google Image search and pull the 23rd result - your students will get over it. Realize that your biggest impediment to productivity is often yourself.

When I run into these self-imposed roadblocks, I have learned to take a step back and analyze what's happening. Usually, my personal hangups are the problem. The next most common problem is the way I'm framing things. When that happens:

Meet the problem where it's at

We all want to solve the Big Puzzle. Why is there violence? What causes depression? Why do people do harmful things to themselves? The Big Puzzle is huge and insoluble by one research project or even one career, so it can be terribly demotivating to expect your work to move the needle. This is because there are too many steps, many of which are unknown, between where the field is right now and the finish line. The solution is to accept that we are where we are, and make as much progress as possible from there as you can.

A colleague has some great advice for this problem. She always encourages me to think about my work in if-then terms: if we knew the answer to this question, then what could we do with that knowledge? I like this advice because it explicitly couches each project as one bridge in the archipelago of the Big Puzzle. Where are we now, and how will this project help us take the next step to where we eventually want to go? I also find it comforting to acknowledge that this one project won't get us all the way there, but, at the same time, to articulate exactly how the project fits into the whole picture.

This advice applies to the Big Puzzle in your field, but also to the littler puzzles of academic life. The task of designing a new course seems daunting because of its scope; meet the problem where it's at (0% complete) by outlining the first week of lectures (>0% complete). If I had an outline, then I could draft the lectures. What is motivating is the blend of knowing that you are making progress toward the bigger goal and feeling like you have a mental map of the little steps you need to take to get there.

More often than we'd like to admit, the next step for the Big Puzzle takes us into uncharted territory. So: 

Get out of your (and your advisor's) comfort zone

Our hamster wheel ensures that the easiest way to get a reward is just to keep doing exactly what we've done in the past. That means using the methods and approaches that are familiar in your lab and to your advisor. But only in rare instances do those just happen to be the perfect tools to address the research question that you think is really important. More often, you need to learn something entirely new to take the next step in answering an important question.

The researchers I most admire all study different topics, but they are all fearless. They don't tame lions or base jump (that I know of), but they do regularly face up to the thing most frightening to academics: the dark emptiness of their own ignorance. It's not that these researchers don't experience the anxieties and insecurities that come with moving into a new area, but rather that they are so deeply motivated to answer their burning question that they are willing to put up with the discomfort. A nice benefit of this is that learning new skills is a skill itself. As you're slogging through a new literature or programming language, you can take comfort in knowing that it'll be slightly easier next time.

My last piece of advice might seem pretty dark and discouraging, but I think it has some overlooked upsides: 

Be willing to leave

Let's have no illusions about this point: academia is a pyramid scheme. That fact has at least three implications. First, very few people make it to the top. Second, each step up becomes increasingly competitive. And third, if that lifestyle makes you miserable, you're probably better off leaving sooner rather than later. This field is not for everyone, and the only thing it definitively says about you if you leave is that you're not into masochism.

This advice is especially relevant to you K-to-PhD folks out there who have gone straight through high school to college to grad school. Academia is not a good default option for most people. Carefully consider why you want to be here. I often ask applicants to our doctoral program why they want to go to grad school. A typical response is “because I really want a PhD.” So why do you want a PhD? “I have always wanted to be a professor.” But why do you want to be a professor? Do you know what professors actually do? “[Blank stare].”

If you can work hard enough to get into a doctoral program, you have lots of options in life. Want money? Go into any number of professional fields and make an order of magnitude more of it than professors do. Want prestige? Go into any number of professional fields and have higher status than us. Want awards? Well, OK, we hand out lots of those.

But what if you want to make a difference in the world? What if you want your legacy to be that you made life better for someone or many someones?

The good news is that, though academia is a pyramid scheme where only a few sit at the top and even fewer have any meaningful impact, science happens throughout society. The skills you learn with a PhD in psychology (or, heck, even after a few years in a doctoral program) allow you to work on the Big Puzzles in many different ways. A researcher at a foundation, think tank, or non-profit can have influence on society far more directly than one at a university. A scientist who affects public policy can change the lives of millions of people. If your real goal is not to publish papers but instead to address big issues, there might be far better opportunities for you outside the wheel.

Elliot Berkman is Associate Professor of Psychology and Director of the Social and Affective Neuroscience Laboratory at the University of Oregon. He also directs Berkman Consultants, LLC. Follow him on Twitter @Psychologician.

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