New students often have difficulty identifying their topic. I provide here some useful heuristics that you can use to think about your topic:
A good topic is usually an intersection between what you are good at, what you are passionate about, and the list of open problems which researchers in your area think it is important.
The key point is to be as specific as possible in thinking about these three dimensions. For example, if you are interested in the brain-computer interface, that can be somewhat too general. You may want to drill down more what specifically triggers your fascination. As for open problems, it is your economic engine, you have to read lots of papers and talk with a lot of people to understand what researchers think is important, NOT what you think is important. Last, think about one specific area where you can be the best of. If you have a background in machine learning, maybe you want to focus on the machine learning aspects of BCI. If you have a background of software engineering, maybe you want to focus on the programming side of BCI.
Try to think of a topic where it will be relevant even after 10 years. You may not want to do any topic that can only last for 1 or 2 years. Research is about thinking ahead. Research comes with greater freedom and the privilege to take higher risk. You may not want to work on “how to increase the battery life of a mobile phone while shrinking the mobile phone size”. This is one of industry work. It does have an important impact but its impact is only short-termed. Distinguish what is industry work and research work. There is an overlap but there is also a clear distinction. You should envision what you want the future to be. Those are the topics you wanna work on. Imagine a topic that you will work even after you finish your Ph.D. for five or more years.
Feasibility (credits: Uri Alon)
The main idea of this diagram is that you can identify your topic based on feasibility. To check feasibility, ask, do you have the skillset to do? Do you have the technology to support your research? Do you have the dataset? Do you have enough time? Do you know how to analyze? Do you think that your work will really 'work'? What are the strengths of your lab and your supervisor?
For beginners like a first-year Ph.D./Master student, it is strongly advised to tackle small, but a significant problem that is relatively easy according to your current skill level + your lab expertise. For example, a small but significant problem could be studying a well-known problem with the well-established methodology but with a slight change in the factors being studied. This small but significant problem is usually published in one single paper. All beginners should start from this - because this will provide you training that requires tackling even harder problems.
Focus on depth (Image Credits: Capella University)
Try to define a narrow problem you can work on. Defining a narrow topic allows you to understand it deeply, vice versa for a wide topic. Ph.D. is about studying one small yet deep problem and comes up with a solid understanding of that very small problem. If you define a wide topic, it does not allow you to scrutinize it deeply and does not allow you to come up with a concrete finding.
For example, doing a topic "Using BCI to control games” is way too wide and will yield too many directions and possibilities where none of them can be rigorously proven in the given time. It lacks focus and depth. In this example, you may want to focus refine your topic more deeply such that you are only investigating one or two factors very deeply. Depth also means that you only have a few objective yet solid metrics that can validate the success of your work.
Remember that Ph.D. focuses depth, not breadth. You can focus on breadth when you get more experienced.
okay, suppose you do all above and you are still stuck in the black hole, you have no idea what is feasible, relevant, nor what is your strength. Do not worry. Try this approach, probably the most pragmatic approach which I termed *High-level copying*. This skill of high-level copying is a philosophy that is based on the idea that the quickest way for any beginners to reach the frontier of an area is to "think" like the giants by "high-level copying" what the giants are doing and improve accordingly.
I found it useful most of the time with any students. Mostly, I recommend all first time Ph.D. student go through once this approach.
The main idea is to learn what the giants/guru/experts are currently doing, what problems they found worthy of solving. Following these giants are likely not going to get you wrong since they have already thought very deeply for over 10 years or more, what are the state-of-the-art problems in a research area. They have a much higher chance to get the topic right, than new Ph.D. students who only spend a few weeks exploring a topic. The process is simple:
First, try to select one recent paper (only one first) you most interested and nearest to what you wanna do, from the conference/journals you want to submit, and make sure that it is ***really good****, this is the key point of whether this method is successful or not (there are some bad papers even in top-tier venues) - check here how to know what are good papers. This will be your model paper. Now, read it several times until you fully understand every little detail, the implementation, experimental design, and every little step in their procedure. Now, this is the core step, try to think what is the core limitation of this paper (tips: usually authors write their limitations and future work at the end of the paper). Based on this limitation, what can you further do to improve? How can you do differently?
Yep, that limitation will be the starting point for your topic.
Definitely, this high-level copying is not only for topic identification but can be applied for your whole study - writing style, experimental design, implementations, related work, and discussion. This high-level copy process is highly efficient but you must know what to copy and what NOT to copy, and if you can master it very well, you are likely to be effective and successful in your beginning Ph.D./Master life.
Anyhow, this approach has some drawbacks, i.e., it limits your creativity but you have to only worry this after you published at least several papers and you are confident enough to explore more risky, unexplored problems. The important thing is that you need to first go through one or two times the entire process of research.
Important points to remember:
- It is important to be flexible, and willing to throw away many “good” topics until you really reach a “great one”. You will typically find that many of your proposed topics will be rejected by the committee or personally by me but rest assured, they are all key steps for you to reach a really good topic. Finding a good problem to solve is already half battle won.
- Leverage the resources your lab have. It will be strange if your lab is specialized at "something" and you opt to work on some other topics. Channel your lab strength to your benefits.
- Note that the problem you care is not as important as the “open” problems researchers care. This is because these open problems are typically key to the field. Doing a problem that only you care will lead to a situation where a tree falls and no one hears it. Find a good balance between these open problems and the problem you care about.
- Related to above is that please do not make-up some problems so that you can argue for the need of a solution. Think deeply is this really a problem? Is it worth solving? Will the result be too obvious such that there is no impact?
- You have a limited lifespan and one cannot be good in everything. Doing everything will lead to nothing. But everyone (yes, everyone) can be great in one or two things. Try to set up a clear goal and focus for your Ph.D. as well as your career. Think of one clear research thing where you are interested at, and that you can do it for at least 10 years or more.
- You may have heard about "follow your passion!", "think outside the box"! but I encourage you NOT to do so. Instead, first explore what already exist in the area, and do it rigorously. You will find that your passion and thinking quickly changes. Only follow your passion when your passion is really well-informed - so important.
- Sometimes it is invaluable to look for inspirations from outside the domain. BCI is an interdisciplinary field and often we can learn a lot from related fields such as pscyhology, neuroscience, machine learning, and human-computer interaction.
- Research is very different from typical bachelor projects. Making something is not necessarily research. You have to think about what is new, how did your work make the world different, if just a little, and how other people (users, researchers, industries) will benefit from your work.
For more readings:
Excellent post what to consider when you choose a topic - http://www.kasperhornbaek.dk/papers/interactions-9questions.pdf
How to choose a good scientific problem? - http://www.imbb.forth.gr/people/aeconomou/pdf/HowToChooseGoodProblem.pdf
What is good research - https://www.cs.utexas.edu/~dahlin/bookshelf/hamming.html
Read this to help you resist tempations of science - http://www.vox.com/2016/7/14/12016710/science-challeges-research-funding-peer-review-process
Complete guide - http://www.cs.ucr.edu/~eamonn/Keogh_SIGKDD09_tutorial.pdf