Review: Alon U (2009). How to choose a good scientific problem. Molecular Cell, 35:726-728.

Feature Paper: Alon U (2009). How to choose a good scientific problem. Molecular Cell, 35:726-728.

Author Abstract: Choosing good problems is essential for being a good scientist. But what is a good problem, and how do you 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 the observation of their teachers. This lack of explicit discussion leaves a vacuum that can lead to approaches such as choosing problems that can give results that merit publication in valued journals, resulting in a job and tenure.

A quick note as this is the first paper we'll review.

1) The above is the general format I'll use to cite the papers I'm reviewing. While citation methods vary by discipline and journal, I'm choosing a fairly standard format: Author Last Name followed by First and Middle Intials (Year Published). Article title. Article Journal, Volume (Number if relevant): Pages. I will follow the full citation with the author's abstract, where available.

2) I will give links whenever possible. For authors, I'll try to give email contacts, though please note that I may not have their most recent contact information in the event that a paper is a few years old or even a classic. I will try to link to the full article whenever it is available for free or at least to the source where you can purchase the full article if you choose. Please note that I am not affiliated with any publishers or scientific journals so I will not benefit from any purchases, so I am not trying to steer anyone in a certain way other than to the path of greater knowledge. I will give a link to the Journal website so you can research other articles as well.

Okay, with that out of the way, let's begin with our review.

Review: I chose this paper as the first paper to cover before getting into headier or more specific topics not only because it is short (3 pages), free of jargon, and freely available on the web, but because often when someone is starting out on the path of science, they take on projects as they are handed to them by their mentors or teachers. However, for those who like to think for themselves, there will often be a problem that interests you. I have learned the hard way that I tend to think about grandiose, multidisciplinary problems that take way too much time to solve. No one taught me to take my enthusiasm and direct it towards smaller, manageable problems that can build together towards a larger goal. After all, a larger scientific goal is just another way of defining a scientific career. But before you can build your career, you must start somewhere. The greatest lesson that I can impart is to pick a theme and stick to it. How you define that theme is based on your personal interests. Oh, and by the way, this applies to life as well. How you learn about that theme through active discovery is what the topic of this week's paper is about.

Summary: The author gives several bullet points to help a young student (or anyone who never learned the proper ways of scientific research) pick a problem that is interesting and adds to scientific knowledge, but that isn't too difficult to research in a relatively short period of time. Before one seeks "Fame and Glory" (in the words of Short Round in Indiana Jones and the Temple of Doom) one should start small and work consistently. Besides, as you begin working on problems, you will invariably discover more questions than answers and one of those questions might turn out to be a big breakthrough later.

Step 1: Choose your problem based on the answers you want to discover in life. What is your theme or goal in science or any other field? You must first establish "values," in the author's words.

Step 2: You must pick a problem based on two metrics: feasibility and interest. Feasibility means defining the problem as difficult or easy to answer, time involved, instruments needed, and basically all the barriers that prevent you from discovering the truth. Later you will learn methods to creatively deal with those barriers to knowledge, but first, you must define your barriers. Interest might seem simple but actually, many scientists don't address problems they are very interested in. Rather, they address problems that either they are given (common for beginning scientists) or they think they can discover the answer to. Yes, there is usually some form of interest, but I can speak from experience. I have become a marine biologist but what I am is a far cry from what I thought I would be when I was younger. Somewhere along the way my dreams got corrupted and I got distracted by the passions of other researchers or exposure to interesting fields and I started studying many different kinds of problems. I learned all too late that this was a mistake, not from gaining varied and interesting experiences in life, but in working toward a single theme and becoming a better and more knowledgeable scientist in my chosen field. As I continue to correct that in myself today, I thought I'd warn you ahead of time. For a young scientist, you probably want to pick problems that the author defines as "easy-but-not-too-interesting low-hanging fruit" kind of problems. But as you gain in experience and confidence, mostly aim for problems with both feasibility and high interest that are "likely to extend our knowledge significantly."

Step 3. Take your time. The author states that before jumping into a project, too many young scientists take the first problem that comes to mind. Just imagine that you follow that path and succeed in solving the first problem. Well, you'll probably discover new problems, which will lead you to other questions, which will lead you to attempt other projects. And soon enough, 10 years go by and you have led an unfocused career and unlikely to have written many scientific papers because you have lacked focus and patience. The author gives the following advice: "do not commit to a problem before 3 months have elapsed." During those 3 months you should read, discuss, and make plans for how you will address your problem. You should understand the feasibility. Taking 3 months will also ensure that the problem is of great personal interest, which fuels the learning process. Don't learn something just because you have to... you should want to learn as well.

Step 4: Subjectivity of interest. Sure, the topic may be of great interest to you but if your inner voice is really calling out to art or literature, maybe science shouldn't be your chosen profession. There's nothing wrong with that. But you can take the techniques of science and the scientific method with you for whatever problem you want to truly address. The author poses the following exercise to help you discover your inner voice: "If I was the only person on earth, which of these problems [that interest me] would I work on?" Answer honestly. After all, the only job you have in life is to discover who you are and what you want to learn.

Step 5: Self-expression. To answer a problem, you need to not only reflect on your personal world view, as the author notes, but I believe you should also learn how to write so that you convey your ideas in a clear manner to anyone reading. Contrary to much scientific writing techniques, you DO NOT have to keep everything in the passive voice. Some of the best papers I've written and the best scientists I've met are very clear about stating exactly what they did, not "what was done." Don't be afraid of this. And don't fall into the trap of using jargon just because you think it is necessary to make your topic appear valuable. Learn the difference between personal and impersonal pronouns. Edit, edit, edit. Keep things short (I know, I have a lot to learn about this, but I'm working on it too). For instance, don't say "in order to" when you can just say "to." There are lots of other little tricks and techniques and I'll try to introduce them as the weeks continue, but in the meantime, start looking online and ask those professors you really look up to. Find those papers that really interest you and that you think are clearly written and emulate their techniques, but remember not to plagiarize.

Step 6: What happens after you choose a problem? The author states that if we pick a problem and outline a path to answer that problem, but we ignore all the other potentially interesting things along the way, we may never succeed (especially if the problems are complex) because we'll continue to get stressed out as our experiments or techniques don't help us solve the problem. Sometimes, the author notes, we should follow our intended path but be open to new problems and developments as they occur. Just remember to only follow the developments that are of true interest to you so you remain focused! In the end, the "answer" we were seeking might not be as interesting as the answer we find along the way.

Hopefully you can use these techniques to pick problems in life that interest you and that build (and rely) upon your skills (which ties into feasibility). Remember to stay focused, but open to new developments. Just make sure that you are always doing what you love in life and don't get sidetracked to the point where you become bitter, disheartened, or let decades slip away.

And always remember, science can be fun and life is about learning.