Are “side projects” self-indulgent?

Many scientists (most?) have side projects; but when we talk about them, we often minimize them in an offhand way – as if we’re just slightly embarrassed to have taken them on. It’s considered somehow virtuous to focus with laserlike intensity on your core research, and a little bit sinful to let yourself be distracted by unrelated side projects.

If pursuing side projects isn’t virtuous, it must be because they waste effort that might otherwise go to your core research. And if they’re “wasting” effort, that suggests that time spent on side projects has a lower return than time spent on core research. Pursuing side projects, then, is self-indulgent: something you do even though you know your lifetime contribution to Science would be higher if you could somehow resist the temptation. I think this belief is pretty widespread (my experience at tenure review suggests so); but is it accurate?

I wondered about that. I’ve had a lot of side projects through my career (to go along with a lot of field-hopping), and I’ve had some oddly conflicted feelings about them. On the one hand, I’ve felt defensive, thinking of side projects as treats I give myself, even though they aren’t as important as my core research. On the other hand, I’ve seen several side projects have substantial impact, and have sometimes even wondered (a bit sadly) if my side projects have had more impact than my core research. These rather contradictory thoughts cry out for data, and so I finally crunched some.

To get a rough measure of impact, I took Google Scholar citation data* for all my publications, and regressed citation counts against years post-publication (the same data and analysis from posts identifying my most overcited and undercited papers). Residuals from this regression indicate the relative impact of my papers, corrected for their age. The result? My side projects have actually had slightly more impact than my core research (graph above), although the difference isn’t significant**.

I could have stopped there, content with the knowledge that my side projects haven’t been self-indulgent wastes of time. But I wondered why. Some ideas:

First, in my core research I sometimes publish less-than-riveting results because I need them as part of a larger scheme. I think of these as “cinder-block” papers; they’re needed for the structure I’m building from paper to paper, but they aren’t lovely by themselves. I don’t expect these to be cited much (although occasionally one surprises me). In side projects, it’s easier to cherry-pick and there’s less need for cinder blocks. However, I don’t think this is the whole story, because dropping all papers with citations < 10 doesn’t change the pattern much.

Second, I might just be lucky. One of my side projects (on what phylogenetic tree shape reveals about ecological controls on diversification rates) hit something of a nerve. It began with a paper I published as a grad student that happened – entirely by chance – to come out just as interest in phylogenetic tree shape was heating up. Later, I moved to UBC as a postdoc and – again entirely by chance – shared an office with Arne Mooers, who was also interested in tree shape, and who’s a superb researcher. Because of that collaboration, I published more tree-shape papers, and they were much better papers than I could have written on my own. I think luck is a big part of the explanation for my side-project impact.

Finally, and distressingly, it might be that I’m really bad at picking core research areas. I’ve argued elsewhere that scientists (especially poorly-funded ones like me) ought to be pretty good at prioritizing their research, to get the most impact bang for their limited buck. But if my core research has no more impact than my side projects, it suggests I’m actually not that good at prioritizing – otherwise, my side projects would be my core. And perhaps I should have made tree shape my core research; my career citation impact might have been higher. Fortunately or unfortunately, though, I wasn’t aware that things would turn out this way; and even with perfect foreknowledge, I don’t think I’d have let citation impact entirely dictate my research direction.***

What’s the take-home message here? I’m not completely sure, but these data seem like a useful reminder that it’s hard to forecast the impact of planned research. We know this at a different scale, of course: it’s why we resist foolish efforts by governments to steer research funding entirely toward short-term commercializable work. In the end, my side-project success – or my core-research mediocrity, if you prefer (which I don’t) – may just be a good illustration of the stochastic nature of scientific progress. Which is one reason it’s so much fun to watch.

© Stephen Heard ( August 25, 2015

*Yes, I know Google Scholar overcounts. Web of Science undercounts (and pretty badly). Fortunately, I’ve yet to find a comparative pattern that doesn’t hold up across the two databases.

**Red lines are means; ANOVA F1,51 = 1.46, P = 0.23 (or F1,49 = 0.04, P = 0.84 omitting the two apparent outliers among side projects). Excluded are publications on which I played a minor role, for instance as a stats-only collaborator.

***Sometimes I do research just because I want to know the answer. Similarly, sometimes I write blog posts just because I want to: my posts on Wonderful Scientific Names don’t get many page views, but I really enjoy writing them, so there will be more.


14 thoughts on “Are “side projects” self-indulgent?

  1. Abigail

    Alternative hypothesis: we choose side projects because of those lucky moments, and we are more selective in them because they will take time away from what we ‘should’ be doing.

    For me, very early-career, the side projects allow me to demonstrate (eg to hiring committees) that I can do more than just work with a single species on a single question.

    What happens if you remove self-citations? If the core work is more incremental maybe there’s a higher rate in that category.


    1. ScientistSeesSquirrel Post author

      Hmm – I didn’t think of that, and left self-citations in. Offhand I don’t think it would change things, because the tree-balance side project has been sustained enough to have quite a bit of self-citation (and my “core” research has shifted enough to be not much more sustained). But I’d have to check the numbers – a project for later!


  2. Ray Becker (@raybbecker)

    Just to copy and paste what I tweeted in reply, “I’ve said it before, but I think unfunded side projects are the real frontier in science. Where does pilot data come from?”

    The data that I got together for a grant awarded to me a few years ago came from a side project. It was something on the side that I just kept prodding my co-authors about until it eventually was funded.


  3. bfavaro

    This is a cool analysis. Speaking from personal experience, side projects have been at least as important to my (early) career progression as my ‘core’ work. In my case, my ‘core’ work (developing techniques to reduce rockfish bycatch in the BC spot prawn fishery) is very specific, and unlikely to ever get cited much. By contrast, my ‘side project’ work has been much more broadly relevant (Fisheries policy in Canada, Species at Risk, and other things). Those get cited more.

    Side projects have been incredibly important in the industrial world. Google is famous for this, with it’s policy that one day a week be spent on something outside of your core job. GMAIL started as a side project!

    Starting at Simon Fraser University, we put together an event we called the ‘Research Derby’ which is an intensive short-term event designed to stimulate side-projects. A colleague and I wrote a little how-to manual: It’s modeled off of ‘hackathons’ in the IT world, and it has worked very well in conservation/ecology when we’ve tried it. Two papers have directly resulted from these events: and – for the Plos One article, we wrote a little blog post explaining how the paper came to be

    Some folks at UW made their own event: – not sure if any papers came from that yet, but they had some very interesting projects from the looks of it.

    My personal opinion is that in grad school when you have one BIG thing that you’re focused on, it can be incredibly refreshing to step completely away from that and apply your skills to something new. Now that I’m a year and a half into my first faculty position, I’m finding that I can’t even really differentiate between my ‘core’ and ‘side’ projects, and the thought of taking on ANOTHER thing is just too much to bear.

    But it’s certainly an interesting thing to think about!


  4. Sarah Boon

    Hi Stephen – just putting here what we talked about on twitter. The contrast between ‘tinkering around’ and Jeff McDonnell’s exhortation in Science Careers to develop a research ‘brand’ is interesting ( It’s obviously worked well for his career, but I wonder sometimes how much is missed (scientifically) with this kind of single-minded approach.


  5. Amy Parachnowitsch

    I probably take on too many side projects because the questions seem so interesting! But comparing the papers coming out of grad school, my most cited is a side-project and it is my most cited paper overall as well. So maybe it isn’t a bad thing to take on side-projects? I guess the main thing is to turn projects into papers, whether they are ‘side’ or ‘core’ research.


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  8. Johannes Knops

    So interesting post. Thinking about this I tabulated up my research period during my Ph. D (1990-1994) and the direct papers published from this in a few years after this.

    Note listed is the journal, year published and citations as of 2015 according to Google.

    Main Ph. D. project started 1990 finished 1994
    Lichenologist 1991 91 Pre-project literature review.
    Ecological Monographs 1996 116 Three year research project all results combined.
    USDA Proceedings 1997 5 Recap of the thesis within a forest management context.
    Total: 212 citations

    Ph. D side project
    Oecologia 1997 54 Examined Nutrient Use Efficiency Theory based on my thesis data. I my mind my best paper within this period. However, looking back I should not have published this paper because it contradicted some very senior person in my field, which did not help my NSF grant reviews in my next ten years. I am also still mystified that the original paper, critiqued here, gets cited much more than this paper that basically shows the pattern in the original paper is just a statistical artifact. As one of my Ph. D committee members said, this is a good paper and should be published, but I do not want to be a coauthor, this is going to upset people. I should have listened to him.

    Total Ph. D project: 266 citations.

    Unrelated side projects
    Biological conservation 1994 91 This paper links species richness among plant communities with plant invasions. Then an obscure topic, I remember the 1993 ESA meeting with exactly 3 talks on biological invasions with all three having lousy data. So looking at my field site I thought I could do a better job, tabulated the data, analyzed it and wrote this up, all in about 2 weeks. The first journal rejected in without review as to trivial, regional, etc. The second journal accepted it after an 18 month review (My longest for any paper ever). This paper was barely cited in the first 10 years, but more after that. (Also, this I should have followed up on, I had a draft of a follow up paper on functional traits related to invasions, but got distracted with other projects and never finished it. Looking back on all the functional trait papers in the nineties and later, bad mistake).

    Southwestern Naturalist 1997 18 totally unrelated to my thesis, drinking beer in my back yard at the field station noticed carpenter bees foraging at night in the dark, thinking this is weird, talked to another graduate entomology student who also thought this is weird, did some observations, drank more beer, observed, wrote paper. Probably the most fun research project that I did so far and it only took a week!

    California Oak project. Walt Koenig was doing acorn surveys looking at oak masting at my Ph. D research site. He is an animal behavior person and talking to him it was clear that I, as a plant ecologist could contribute something to this project, and he is a fun guy, so I got involved during my Ph. D time and ever since.

    Canadian Journal of Forest research 1994 87 method paper cited for many follow up spatial synchrony papers.
    Plant Ecology 1997 47 Linking soil fertility to oak trees.
    USDA Proceedings oak 1997 5
    California Agriculture 1995 14
    Madrono 1994 13
    Madrono 1996 3
    And many more highly cited papers since.
    Total : 278

    So, looking back, my site projects during my Ph. D have been much more influential that my main research project so my advice, be opportunistic and take advantage of anything interesting that you notice.

    Cheers, Johannes Knops


    1. ScientistSeesSquirrel Post author

      Johannes – thanks for commenting, and it’s nice to see that I’m not the only one with this pattern! Your experience with the nutrient use theory paper is troubling but not terribly surprising – I think there are other examples of “debunked” patterns still being cited more than their debunkers are. I bet you anything Jeremy at Dynamic Ecology has a post about this 🙂


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