Dept. Molecular Cell Biology, Weizmann Institute of Science
Choosing good problems is essential for being a good scientist. But what is a good problem, and how to choose one? The subject is not usually discussed explicitly within our profession. Scientists are expected to be smart enough to figure it out on their own and through observation of their teachers. This lack of explicit discussion leaves a vacuum that can lead to approaches such as: choose problems that can give results that merit publication in valued journals, resulting in a job and tenure.
The premise of this essay is that a fuller discussion of our topic, including its subjective and emotional aspects, can enrich our science, and our well-being. A good choice means that you can competently discover new knowledge which you find fascinating and which allows self-expression.
We will discuss simple principles of choosing scientific problems that have helped me, my students and many fellow scientists. These principles might form a basis for teaching this subject generally to scientists.
What is the goal of starting a lab? It is sometimes easy to pick up a default value, common in current culture, such as "the goal of my lab is to publish the maximum number of papers of the highest quality."
However, in this essay, we will frame the goal differently: "A lab is a nurturing environment that aims to maximize the potential of students as scientists and as human beings."
Choices such as these are crucial. From values, even if they are not consciously stated, flow all of the decisions made in the lab, big and small: How the lab looks, when students can take a vacation, and – as we will now discuss - what problems to choose. Within the nurturing lab, we aim to choose a problem for our students (and for ourselves) in order to foster growth and self-motivated research.
To choose a scientific problem, let us begin with a simple graph, as a starting point for discussion. We will compare problems by imagining two axes. The first is feasibility, that is -- whether a problem is hard or easy, in units such as the expected time to complete the project. This axis is a function of the skills of the researchers and of the technology in the lab. It is important to remember that problems that are easy on paper are often hard in reality, and that problems that are hard on paper are nearly impossible in reality.
The second axis is interest: the increase in knowledge expected from the project. We generally value science that ventures deep into unknown waters. Problems can be ranked in terms of the distance from the known shores, by the amount in which they increase verifiable knowledge. We will call this the interest of the problem.
In a forthcoming section, we will discuss the subjective nature of the interest axis. But first, let us first consider aspects of problem choice using our diagram.
Looking at the range of problems in this two dimensional space, one sees that many projects in current research are of the easy-but-not-too-interesting variety, also known as 'low hanging fruit'. Many other projects in science today are unfortunately both difficult and have low interest, partially stemming from a view that hard equals good. A few problems are grand challenges: tough problems with the potential to considerably advance understanding. But most often we would like problems in the top right quadrant, both feasible and with high interest, likely to extend our knowledge significantly.
The diagram suggests a way to choose between problems, using the Pareto front principle of optimization theory. If problem A is better on both axes than problem B, one can erase B from the diagram. Applying this criterion to all problems, one is left only with problems for which there are no problems clearly better in both feasibility and interest. These remaining problems are on the Pareto front.
To decide which problem to select along the front depends on how we weigh the two axes. For example, a beginning graduate student needs a problem that is easy: positive feedback can thus be rapidly provided, bolstering confidence. These problems are on the bottom right of the Pareto front. The second problem in graduate school can move up the interest axis. Postdocs need projects in the top right quadrant, since time is limited. Beginning PIs, that need to select a field on which to spend at least ten years and with which to train students, may seek a grand challenge that can be divided into many good, smaller projects. Thus the optimal problems move along the Pareto front as a function of the life stages of the scientist.
A common mistake made in choosing problems is taking the first problem that comes to mind. Since a typical project takes at least two years even it if seems to be doable in two months, rapid choice leads to much frustration and bitterness in our profession. It takes time to find a good problem, and every week spent in choosing one can save months or years later on.
In my lab we have a golden rule for new students and postdocs: do not commit to a problem before three months have elapsed. In these three months the new student or postdoc reads, discusses, plans. The state of mind is focused on being rather than doing. The temptation to start working arises, but a rule is a rule. After three months (or more), a celebration marks the beginning of the research phase - with a well planned project.
Taking time is not always easy. One must be supported to resist the urge "Oh we must produce, let's not waste time and start working". Taking time can be especially difficult when funding is insufficient and grant deadlines approach. In such difficult situations, nurturing is not enough, and you need to find support and do all you can to get into a better situation. Even so, for many of us dealing with the difficulties of running a lab, taking time to choose problems can make a huge difference.
Let us now look in more detail on the axis of problem interest. Who decides how to rank the interest of problems? One of the fundamental aspects of science is that the interest of a problem is subjective and personal. This subjectivity, however, makes things confusing. The confusion is due to the mixing of two voices - one is a loud voice of the interests of those around us, in conferences, in our department etc. The other is a faint voice in our breast, the voice that says "This is interesting to me". Ranking problems with consideration to the inner voice makes you more likely to choose problems that will satisfy you in the long term.
The inner voice can be strengthened and guided if one is lucky to work with caring mentors. A scientist often needs a supportive environment to begin to listen to this voice. One way to help listening to the inner voice is to ask: "If I was the only person on earth, which of these problems would I work on?" An honest answer can help minimize compromises.
Another good sign of the inner voice are ideas and questions that come back again and again to your mind for months or years. These are likely to be the basis of good projects, more so than ideas that have occurred to you in recent days. Another good litmus test: when asked to describe our research to a new acquaintance, how does it feel to describe each project?
It is remarkable that problem choice based on listening to our own idiosyncratic voice leads to better science. It makes research self-motivated and the routine of research more rewarding. In science, the more you interest yourself, the larger the probability that you will interest your audience.
What is the essence of the inner voice? The projects that a particular researcher finds interesting are an expression of a personal filter, a way of perceiving the world. This filter is associated with a set of values: the beliefs of what is good, beautiful and true versus what is bad, ugly and false. Our unique filter is what we bring to the table as scientists. A multiplicity in styles and questions, based on the uniqueness of scientists, is the basis of a viable and creative science.
To choose a good problem, therefore, we need to reflect on our own world view. And as mentors, we can help students in the late phases of their PhD or in the postdoc stage to strengthen their inner voice. A mentor can help by listening to a student describe what they like in science, in life outside of science, what moment made them decide to become scientists, what scientific work they admire. We sometimes begin to see patterns in what the student is talking about. There emerges a map of values, in the way that deep rocks in an ocean are discernable by the waves made on the surface. Is this student motivated by visual aesthetics or by abstract ideas? By supporting the dogma or by undermining commonly held truths? Likes techniques or logical proofs? Basic understanding or applied work? And so on. This can help the mentor select a project in which the student has the potential for self-expression. As mentioned above, when one can achieve self-expression in science, work becomes revitalizing, self-driven and laden with personal meaning. It may also have a better chance of discovering something profound.
What happens after we choose a problem? Before we end, I'd like to discuss the mental picture or schema we hold of what research will look like. A common schema is expressed in the way papers are written: one starts at point A, which is the question, and proceeds by the shortest path to point B, the answer. There is a danger, if one accepts this schema, to regard students as a means to an end (an arrow to B). Furthermore, for those that hold this schema, any deviation from the path (experiments that don’t work, students that become depressed etc) is intolerable. Deviation causes stress because of the cognitive dissonance between reality and the mental schema.
However, one can adopt a second schema, one that resembles more the course of most projects. As before, one starts at point A and moves towards the goal at point B. Soon enough, things move off course, the path meanders and loops back. Experiments stop working, all assumptions seem wrong, nothing makes sense. The researcher has entered a phase linked with negative emotions that may be called the cloud.
Then, in the midst of confusion, one senses a new problem in the materials at hand. Call this new problem C. If C is more interesting and feasible than B, one can choose to go towards it. After a few more detours, C is reached. The researchers can pause to celebrate, before taking time to think about the next problem.
In this second schema, the typical meandering of research is seen as an integral part of our craft. The mentors' task is to support students through the cloud that seems to guard the entry into the unknown. And with this schema, we have more space to see that problem C exists and may be more worthwhile than continuing to plod towards B. In this way, choosing a problem is like entering a garden, with many diverging paths, until, walking down a trail, one glimpses a side path with a beautiful rose.
In summary, take your time (3 month rule) to find among the problems available the one that is most feasible with your skills and resources and most interesting to you rather than to others. A good project draws upon your skills to achieve self-expression.
For more Materials for Nurturing Scientists, see http://www.weizmann.ac.il/mcb/UriAlon/
The ideas in this essay were presented to me as gifts in conversations and books, or are the fruit of learning from my mistakes, and are collected here and again offered as a gift. Especially memorable are discussions with Ron Milo, Galit Lahav, Becky Ward, Yuvalal Liron, Michael Elowitz, Angela DePace, Evelyn Fox Keller and her writings, especially 'Reflections on Gender and Science', and with members of my lab and colleagues who told me stories of mentoring and problem choice. My parents, my partner Galia Moran and my daughter Gefen, and mentors I. Balberg, Dov Shvarts, David Mukamel and Stan Leibler. Harvard's Psychology 1501 taught by Tal Ben-Shahar, 2008. Dan MacAdams for his books 'The Person, a new introduction to personality psychology' and 'Narrative lives', Amir Orian and The Open Circle approach to creative arts, classes of 2005/6, Jonathan Fox for playback theatre and his book 'Acts of Service', Jerome Bruner for his book 'Acts of Meaning', Erik Erikson for 'Childhood and Society'. The Weizmann Institute for providing freedom to play. Mark Kirschner and the Harvard Medical School department of Systems Biology for hospitality and a place to discuss these ideas with a well-prepared audience. Critical remarks by audience members in Janelia Farms who helped sharpen the message.