5 Steps for Keeping Motivated in Graduate School

Note: This is part 2, a continuation of my reflections on lessons learned in graduate school so far.

One of the lessons I have learned over the past three years of grad school is that a graduate student has to have some form of motivation that keeps us going. The moment we get disengaged with the work that we are putting our time and effort into is the moment that we begin the downward slide in our graduate career.

I believe that one of the things that keeps a student going is to have a vision for what the end result of their project might look like. In this blog post, I’m going to assume that we know why a vision is important. Therefore, I will instead answer how I think vision develops, and along the way, propose a gentler definition of what it means to have vision, especially for those who are starting out in graduate school.

Start by understanding what problems are valuable.

At the initial stages of developing a thesis, reading is exceedingly important. With reading, we begin to understand what problems are worth tackling, and what problems are not worth tackling. We’re doing a PhD – why would we tackle something not worth tackling?

For example, my current thesis work began as this hazy idea of classifying influenza viruses and then using synthetic biology DNA manipulation techniques to systematically create a BioBank repository of viruses, which could serve as a source for vaccine production. While it sounded really cool and useful to me, I soon came to realize that there were many infeasible components to this idea, especially as a project for a PhD student to undertake. As I read more and more about the influenza world, I realized that the problem of viral antigenic shift through reassortment was a more valuable problem to tackle than creating a BioBank. I thus began thinking about how I would go about measuring the amount of reassortment worldwide, eventually settling on the methods that I’m developing right now (shhhh! It’s secret until I publish it! :D).

Know the problem you’re tackling and state it in clear terms.

The beginning of our thesis work starts with identifying a novel, challenging and valuable problem to tackle. But is it possible to know what shape and form this problem will look like right from the beginning? Absolutely not! Expecting that is akin to expecting a three-year old child to envision himself or herself as a world class piano performer. Vision does not come like that. I think we need to have a more forgiving expectation of how vision comes about, one that is in line with the natural growth that we experience.

I believe that having a vision for our project first starts at clearly articulating a problem statement. For my PhD thesis work, that meant clearly identifying the quantitative question that I was going to answer. One of my aims started off this way: “What proportion of influenza viruses isolated in a population of wild birds at a field site are reassortant viruses?” There are a number of salient features of this statement. Here they are:

  1. The problem statement looks like it can be tackled within half a year.
  2. The problem statement has a number that I can deliver as an answer.
  3. The problem statement is limited to a model system (wild birds), which helps me focus the context in which I am operating.

It’s important to have an initial problem which can be answered quickly, which also has a hint of novelty, difficulty, and value. This is hard to grasp early on, which is why PhD advisors exist – their experience can provide us with a very good guide. It’s also part of the entrepreneurial side of graduate school work – “fail fast, fail early” is the mantra. If I cannot deliver on the problem statement within the first six months of proposing the problem, it’s probably too difficult for me to answer.

Iterate between drawing your strategy and executing it.

Drawing out my proposed strategy for answering my problem proved to be immensely useful for me. What it did was force me to take my proposed method and boil it down to its essentials.

However, I think one shouldn’t have a completely fleshed out strategy before embarking on it. I see risks to taking this route:

  • We may become too emotionally invested in our ideas (always unhealthy – one’s value is not determined by one’s ideas).
  • We become blind to the hard spots in the method (wasted time).

There may be more, but at 9:52 pm (time of writing this paragraph), I can’t think of them. I think one’s strategy should be fleshed out just to the extent that stretches our ability to anticipate problems, and then we execute on it in the cheapest fashion possible that delivers the maximum lessons learned. Cheapest means in terms of time, manpower, money etc. Lessons learned means new knowledge that helps us refute or support assumptions that we’ve made, so that we can adjust our strategy. We may not be able to anticipate new insights, but if we are prepared to look for them in our results, they can also become a part of the lessons learned.

Once we execute, we will find out where the flaws in our initial plan are. That can help us when we go back to the drawing board, to identify where to make changes in our strategy. Which then feeds back into another set of lessons learned from trying.

In the case of how I was planning to tackle the problem of how much reassortment happens in wild bird populations, started by drawing out how I thought reassortment happens, and then pitched the idea to my colleague about using a subset of only 20 viral isolates. I then drew out by hand how I thought those viruses would be represented in a figure showing reassortment, as a result of trying to identify the reassortant viruses. I still keep scanned copies of that original idea. Following that, I began implementing my idea in Python code, which then revealed to me where I was going to encounter difficulties if I were to scale up to larger datasets. That forced me to go back to drawing, to illustrate to myself, my colleagues, and my advisor & committee how I could work around those problems. (again, I won’t say more until it’s all published!)

Along the way, evaluate how the idea can be expanded.

With time, we begin to see how our original idea can be expanded. Parts of what we do can be leveraged for other applications. Alternatively, we may be able to generalize beyond the original model focus.

In my case, my advisor Jon continued to remind me that I was able to think beyond the influenza virus, and into other segmented RNA or DNA viruses. In addition, my own ambitions were to be able to tackle the entire influenza dataset, rather than limit myself to wild bird viruses. I also began to see other smaller problems that could be tackled using modifications of my proposed method, some of which may be interesting detours for publication that would still build the case for my bigger ideas. In other words, I think we ought to take the technical aspects of our project, and see how they can be leveraged for other

Grand vision is knowing why and how your project is relevant and useful to the most number of people possible.

In other words, it’s knowing how your current project can make a positive impact in the world. I believe that this takes many years to become realized, so it’s unreasonable for us to expect that we can achieve it within our PhD. That said, we only have much to gain and nothing to lose trying to do so!

In my project, I’m seeing that the ability to identify reassortant viruses quickly and in real-time can really make an impact in our viral surveillance efforts. Reassortant viruses are the ones that have the greatest potential to cause human disease. I’m envisioning that what I develop can become a part of a software dashboard that can help epidemiologists make better recommendations on where we need to prioritize vigilance and monitoring, given the limited resources available in outbreak hotspots. If I can develop that dashboard, I would totally love to! However, if I cannot, at least I’ll have made my mark with a component of the dashboard.

However, I also live in the tension zone between knowing that my current vision may be ultimately unattainable and being willing to change it, while still dreaming about the vision becoming true. I think of this tension zone as the high-functioning zone, somewhat akin to what’s described in this article. I believe that the earlier we can become comfortable in this zone, the earlier we will be on the path to awesomeness.


To recap, here’s the main steps to developing a great vision for your project:

  1. Start by understanding what problems are valuable.
  2. Know the problem and state it in clear terms.
  3. Iterate between drawing the strategy and executing it.
  4. Along the way, evaluate how the idea can be expanded.
  5. Know why and how your project is relevant and useful to the most number of people possible.

I believe that the most salient feature of this process is that it started small. Really small. Like a mustard seed that eventually grows into a large plant – but starts small. Most of the best companies I’ve seen have really small and focused roots. They then expanded by either generalizing or by leveraging, or doing both at the same time. But it takes a tremendous amount of focus early on, to deliver results that can be leveraged for more resources to do bigger things. Just as how entrepreneurs do it, PhD students ought to be doing the same. The vision gets clearer and clearer – and evolves with the results that get delivered.

Having written all this, I’d also add that I will gladly admit that I’m nowhere near completion. I’m only in my 4th year in graduate school. My road ahead is still long! (well, hopefully.) From where I’m standing right now, I believe that vision is developed along the way, organically, and while it should be inspiring, it should not be overly fixed and rigid in the early stages. I believe it’s only 10-15 years from when we start, when we have the winning combination of:

  • a track record of results to inspire confidence,
  • experience of enough failures to cultivate humility,
  • a large and diverse enough network to leverage, and
  • a well developed and concrete vision

will we be able to really influence and become a mover and shaker in the greater community. For now, though, I’m happy to build my track record right here, right now.