04 November 2019 on posts
This blog is also posted on the POLISES website.
A woodsman was once asked, “What would you do if you had just five minutes to chop down a tree?” He answered, “I would spend the first two and a half minutes sharpening my axe.” 
So it felt when I began my short-term research stay as a visiting PhD student at the Helmholtz Center for Environmental Research (UFZ) in Germany. I had three months, and the goal was to produce a draft version of a paper by the end. As any young, ambitious scientist, I was eager - yet slightly anxious - for the challenge.
To give some context, my research involves building simulation models (agent-based models - or ABMs) that describe social-environmental systems. I apply these models to explore questions related to resilience in smallholder agricultural systems. During my research stay at UFZ I was hosted by the POLISES (Policy Instruments and Social-Ecological Systems) research group in the Department of Ecological Modeling. In contrast to my home department in the USA, the domain-relevance of the POLISES team was a refreshing change.
But the POLISES team also had a slightly different approach to formulating research projects than I was used to. Being exposed to this different perspective, as well as the feeling of time pressure to actually accomplish something in three months, helped me to learn a few lessons that I hope to continue to integrate into my future research career. Although some of these lessons may be specific to me (and were things that I had been trying to learn for a while), I think that more generally the opportunity to temporarily step away both physically and mentally from one’s regular dissertation research can be an enriching experience.
This was my biggest source of frustration during my first few weeks. But it also turned out to be perhaps the most important lesson that I learnt (and hence I have the most to say about it). The POLISES team believe strongly in formulating specific and measurable hypotheses to guide a modeling-based research project. In my previous research, I focused on identifying “research questions” to frame and focus my work. I was interested in using modeling to explore “the conditions under which” certain outcomes can occur or “identifying the most important factors” driving an outcome. These types of questions are undoubtedly relevant and important, but I have learnt that having a hypothesis can simultaneously add clarity and depth to these questions.
Akin to the woodsman sharpening his axe, a well-thought-out hypothesis helps to refine the scope of the model and analysis. The shift in perspective is fairly subtle (in my interpretation); rather than exploring the “conditions under which Y happens”, a hypothesis-driven approach will hypothesize that “under X conditions, Y happens”. My experience with research questions was that they may appear to be specific, but it is difficult to know when they have been answered and hence when to stop. Admittedly, this was partially because I hadn’t been asking “good” research questions, but formulating a hypothesis had a somewhat transformative effect; hypothesizing what my results might show was in effect answering my research question at the same time as posing it. It also required having an idea, based on theory and previous evidence, about the processes that might lead to an outcome (see Lesson 3). Rather than being left to explore seemingly endless “conditions under which” things may happen, all I had to do was test whether or when my hypotheses (about specific conditions) were true.
However, having a hypothesis also can imply having a preconceived idea of what you “want” your results to show. It’s therefore important to take precautions to not let this happen. Although the purpose of hypothesis “testing” is to assess the potential for the hypothesis to be falsified, the flexibility of process-based modeling (and even statistical modeling of empirical data, I would argue) gives the researcher the power to change things “behind the scenes” until they see what they want - or what they believe the high-impact journal will want. I’m still figuring out the best ways to guard against this in my research. I like the concept of Strong Inference , which argues for having multiple working hypotheses and designing experiments to successively exclude them, but I’m yet to implement this myself.
As an additional caveat: this lesson is likely not generalizable to all types of research projects. My experience here has taught me about the power of the hypothesis in agent-based modeling research. I truly believe it is important in this field. But I am still learning. I imagine that in, for example, exploratory research, methodological research, or for review articles, hypotheses are not as relevant. As I begin new research projects in the future, I look forward to experimenting with the “conditions under which” posing hypotheses is the most useful.
Throughout my PhD I have engaged in lots of “side projects”. These have been exciting and added diversity to my experience, but I have found that they can take away from the quality and thought I can give to my main projects. Being employed at UFZ with the specific aim of working on a single project helped me to focus; I treated it like a 30 hour per week job, spending this time exclusively on my main UFZ project, and only working on side projects in any time that remained after this. Carving out regular portions of my days to work on a single project gave me more headspace than if I was budgeting time between projects on-the-fly. This headspace allowed me to think more deeply about the project at a high level before diving into it. Similarly, I found that having slack time budgeted for my main project gave my brain room for more creative thinking that inspired ideas I maybe otherwise wouldn’t have had. Side projects definitely have their place, but by keeping them on the side, it’s possible for them to not exist to the detriment of what you’re meant to be doing.
A lot of research aims to answer the general question of “what is the effect of X on Y”. Knowing this is critical for understanding how systems may behave under different conditions. However, what is more interesting is knowing why systems behave as they do. A move away from assessing effects to understanding mechanisms is common in many research areas these days. In my case, I had previously developed a model that was very complicated. Simulation models are a seductive tool after all - it’s possible to include everything under the sun in your model. However, in doing so, it becomes more difficult to understand and explain what leads to your results. In most cases, agent-based models are not intended to be predictive. You can’t model everything in the world. So don’t attempt to. Focus on your question/hypothesis, and include only what is critical to represent that. And don’t stop when you have results - use your model to explore why those results came about.
We all want to publish in the top journals. The thought of it is very alluring. This lesson has been a long time coming for me, but here was the time for me to learn it. Unless what you have is really remarkable, don’t let yourself be fooled by it (too much). Don’t let a lusty desire to break the ground with your first ever research project waste your time. Be realistic in the journal that is appropriate, and design the research with that in mind. Maybe it takes being rejected to come to terms with this. Or maybe it just requires stepping back and remembering that this is your PhD and there is plenty more time to be publishing in top journals and making waves. You should learn how to do solid research during your PhD, and build your way up to more flashy things later on.
I think this one is quite obvious. Spending time with people that are not also in academia is a good reminder that not everything is about research. This can add perspective to your life.
Overall, I would highly recommend doing a research-based “internship” during your PhD. I found it incredibly instructive to take a few months away from the daily grind to experience research in a different context. Like the woodsman, by stepping back I was able to reflect on the task at hand, sharpen my tools (models), and target the right trees (questions/hypotheses). I look forward to applying these lessons in my future research and comparing my experience with others to see to what extent these lessons are generalizable.
PS: please don’t cut down all the trees
 1956, Increasing Understanding of Public Problems and Policies: A Group Study of Four Topics in the Field of Extension Education, “Objectives and Philosophy of Public Affairs Education” by C. R. Jaccard, Start Page 12, Quote Page 12, Published by Farm Foundation, Chicago, Illinois. (Verified on paper)
 Platt, John R. 1964. “Strong Inference.” Science 146 (3642): 347–53.