FAQ for Grad Students

"Your primary responsibility as a doctoral student is to generate high-quality ideas and bring them to successful completion. Sounds straightforward, but there is a catch: you're not explicitly taught how to produce ideas or navigate the process of writing an academic paper. In this note, I discuss some insights I wish I had known at the beginning of my Ph.D. journey about the first of these two tasks. Specifically, I discuss some practices that can aid the idea-generating process, strategies for filtering out less-promising ideas, and decision-making heuristics to determine which projects are worth pursuing." - Germán Reyes

"The process of generating ideas often shrouds itself in mystery. In the midst of a routine day, a sudden spark might ignite in your mind. Perhaps it's the connection of a point made in a recent presentation to a paper you perused ages ago. Together, they decipher a puzzle in your field. You find yourself thrilled: this has the potential to become an exceptional research project. But where did this train of thought originate from? Who knows.

Personally, I've found that ideas often come around serendipitously. I have had ideas (granted, mostly bad ones – but I'll delve into that later) amid casual conversations, seminars, skimming the news, running, and more often while reading papers and books. Paradoxically, ideas rarely come from the standard “directions for future research” paragraph in the conclusion of papers, where authors typically contemplate extensions that are not particularly exciting or are challenging to implement.

Several of my research projects have crystallized by integrating ideas from seemingly disparate sources. A prime illustration of this serendipitous process is my job market paper, where I delve into the role of cognitive endurance in the labor market. This paper’s inception can be traced back to three different content sources.

Initially, I was intrigued by a series of blog posts written by computer scientist Cal Newport, whose work I have followed for a long time. During my early years of grad school, Newport started discussing the concept of “Attention Capital” (see, for example, here and here). He proposed that the capacity to maintain focus on cognitively demanding tasks is a key source of capital for workers in the knowledge economy. This hypothesis resonated with me — it matched my intuition that being able to do hard work for a long time should have a large payoff in the labor market. But at the time, it did not occur to me that this topic could be the material for a paper, so I filed the idea away.

Fast forward to my fourth year, when I attended a presentation by Heather Schofield on a paper then-titled "Attention as Human Capital,” later rephrased as "Cognitive Endurance as Human Capital.” Schofield and her coauthors show that individuals' performance tends to degrade over relatively short time spans in diverse environments. They posited that cognitive endurance, the capacity to persist in cognitive tasks over time, is a skill that can be trained. To validate this hypothesis, they conducted a randomized control trial, which yielded supportive evidence. The paper contained numerous intriguing discoveries, but what captured my attention was the notion that cognitive endurance—the concept Newport discussed—can be empirically measured by assessing the rate of individuals' performance decline.

If Newport's hypothesis was correct and cognitive endurance makes workers more productive, then one could use a performance-decline-based measure to test whether workers with more endurance earn higher wages, as standard models would predict. The challenge boiled down to finding a dataset where one could measure cognitive endurance and labor market outcomes for the same set of individuals.

The puzzle pieces fell into place when I found the right setting. During a research assistantship, I was introduced to the rich world of Brazilian administrative datasets and, particularly, the Brazilian college admission exam known as the ENEM. This exam provides an excellent setting to study cognitive endurance due to its uniform administration, high-stakes nature, and grueling length (ten hours over two consecutive days). Most importantly, the exam records contain question-level data (essential for tracking the change in students' performance) and can be linked to an employee-employer matched database (necessary for linking endurance to earnings).

This perfect confluence of circumstances enabled me to finally operationalize and test the hypothesis that cognitive endurance, as a form of human capital, indeed has a significant impact on labor market outcomes." - Germán Reyes

"The journey behind my job market paper is intricate and far from linear. But by no means the story is unusual. Many of my other projects also had convoluted origin stories, and many of my colleagues recount parallel experiences.

Confronted with the inherent unpredictability of this process, it's tempting to conclude that the generation of ideas relies heavily on luck, leaving little within our control. I do not think this is quite right. There are practices and strategies one can adopt to catalyze and nurture idea generation.

The first step is acknowledging that ideas can spring from unexpected sources. In his book "Where Good Ideas Come From,” Steven Johnson characterizes an idea as a network of neurons. Novel ideas are born from fresh neural connections, often linking and recombining topics that might appear unrelated in the abstract. Thus, fostering serendipity and new connections requires exposure to high-quality ideas. This can be achieved in numerous ways. For instance, a colleague of mine scheduled regular lunches with fellow Ph.D. students to discuss research, a practice that led to at least two top-field papers. Other strategies could involve attending seminars outside your field, interacting with people from diverse backgrounds, or reading nonfiction books with an eye for findings from other disciplines or social sciences that can yield unexpected insights into your field.

I strongly advocate maintaining a document where you record every noteworthy idea you encounter. A brief summary of each idea—one or two sentences—should suffice. Ideally, there should be little friction in storing your ideas (I have an easily accessible notepad file titled “ideas-list.txt” and always carry a small notebook with me). Otherwise, you run the risk of ditching the system altogether. For each idea, you can also have an associated folder where you can drop relevant materials that you come across, such as related papers or motivating examples. Keeping a record of all your ideas is beneficial for a few reasons. It frees you from relying on your memory when you wish to revisit an idea, facilitates making connections between different ideas, and over time, you can observe how your ideas evolve and become more "refined."

If things go right, your ideas document will have far more potential projects than you can possibly have time for. For most of us, the majority of the ideas on this list will be unusable, often because others have previously explored them or because most ideas, quite simply, are plainly bad. That is to be expected. I like to think of the idea-generating process as drawing from a distribution: each idea is a fresh draw from the "idea distribution." Before you pull an idea from the right tail of the distribution, you'll likely have to churn through numerous less stellar ones. The key to generating good ideas is to generate plenty of ideas. But how do you distinguish the worthy from the worthless?" - Germán Reyes

"Physicist Richard Feynman astutely remarked, "The first principle is that you must not fool yourself, and you are the easiest person to fool." This wisdom particularly applies to evaluating the merit of our own ideas. We tend to develop an attachment to our ideas, mirroring the well-documented "endowment effect" in behavioral economics. This emotional investment can make distinguishing between good and bad ideas one of the most challenging aspects of the research process—we often believe our ideas are good simply by virtue of being ours.

Because we are often poor judges of our ideas, a good practice is to get external feedback, essentially "outsourcing" the evaluation process. For instance, during my third year in grad school, I had weekly meetings with my advisor to discuss 3-5 paper ideas (it is worth highlighting that my bar for what constitutes a “paper idea” is pretty low). Most were, to put it mildly, garbage. But those meetings helped me to make sure those ideas were bad, and two of the ideas that survived those meetings eventually became my third-year paper and my job market paper.

Similarly, my advisor told me the story of how George Akerlof used to screen good from bad ideas. Every morning, he would pitch Janet Yellen (Akerlof's wife) a handful of ideas. Most mornings, Yellen would dismiss them. But every now and then, she would tell him an idea had potential, and that's how he knew which ideas to pursue.

It should be emphasized that while those providing feedback often have your best interests in mind, they are not immune to biases. Their preferences for particular topics or methodological approaches may influence their feedback. For example, in one project, my coauthors and I run a lab experiment to understand how inequality of opportunities affects income redistribution. I often failed to enthuse public economists because many were skeptical about the external validity of lab experiments in this context or not interested in inequality. Thus, I recommend "pitching” an idea to a diverse audience before deciding to pursue or abandon it. If most individuals are unimpressed, this might signal that your efforts could be more productively deployed elsewhere." - Germán Reyes

"After passing the qualifying exams, I felt the need to get involved in as many projects as possible. I pitched ideas to everyone and said yes to any invitation. This was partly due to the allure of brainstorming and idea exchanges, which is often more fun than the rigorous work necessary to implement them. But also because I was incredibly (and still am) concerned with a “fear of missing out.” I was so hungry to show I was worthy (as a researcher, and I felt that, by extension, as a person) that I didn't want to say no to any opportunity.

Just like me, I know many people who, at some point, get involved in more projects than they can possibly think deeply about. But saying yes to every opportunity is not a sustainable project-selection criterium. As a rule of thumb, one cannot do serious thinking in more than two to three projects at a time.

So, how should one choose which projects to commit to? One naive approach is to choose projects that seem exciting. The problem is that the initial excitement often fades away, and predicting which project will sustain interest over the long term is challenging given the evolving focus of projects and of your own interests.

Still, there are a few practical heuristics that I have found valuable to navigate the selection process.

First, implement a “cool-off” period before making a long-term commitment. This allows your "future self” to evaluate the potential research project with a more detached, objective perspective. A project that initially appears ground-breaking may lose its charm after some weeks—or after a thorough literature review. One piece of advice I received from a committee member is to set a low bar for initially exploring the potential of a project (say, a week to calculate some descriptive statistics and basic regressions) but a high bar to commit to an actual project.

Second, don’t underestimate the amenities of a project. It's common to choose projects based on their perceived publishing potential (“Is this top-five material?”). But there is much more than that to a project. First, a paper allows you to think deeply and consistently about a problem for years.  Thus, it is sensible to choose a subject you’re genuinely interested in. Second, collaborative projects give you a chance to interact with others frequently. This can be extremely rewarding if you admire and get along with your coauthors (the converse is also true, so be careful while choosing whom to collaborate with). Third, projects outside your “range” allow you to learn new skills and subjects. For example, as an empirical economist, collaborating on a signaling paper with a theorist forced me to learn about signaling models and the fundamentals of model building.

Finally, adopt a “long view.” If you consider being involved in one major project per year (an ambitious number by most accounts) over a forty-year career, this amounts to forty main research projects in a lifetime. When considering a new project, ask yourself: "Is this of those forty?" If not, taking on a mediocre project may hinder the opportunity to undertake more promising ones in the future. While not all projects need to be ground-breaking, I do think all projects need to be chosen deliberately.

The journey of generating ideas and turning them into high-quality papers is both complex and multifaceted. It starts with fostering serendipity and seeking diverse sources of inspiration, creating an environment conducive to the birth of novel ideas. These ideas are then curated and filtered through reflection and external feedback, distinguishing the promising from the mediocre. The next step, committing to a project, involves evaluating not only the idea's potential academic contribution but also personal factors like sustained interest, collaboration potential, and opportunities for professional growth. These principles underscore the importance of strategic thinking in navigating the challenging yet rewarding path of academic research." - Germán Reyes