One of the most common questions I get asked is how to choose a thesis topic or research project. Unfortunately it’s not as simple as just “finding a gap in the literature”, and there are many complicating factors to consider. In this excerpt from the book, “PhD: an uncommon guide to research, writing & PhD life”, I outline what you need to know…
There’s a lot to consider, so take your time reading this!
What makes a good project?
Good research depends on many factors, and a good idea alone is not enough.
You can have a brilliant idea, but the ultimate quality of the research will depend on your execution; an average idea well-executed is much better than a brilliant idea executed badly.
In turn, your ability to execute the research will depend on your specific research skills (existing and developing), as well as your access to other resources such as equipment, funding, technical support and time. Since these factors vary greatly, what may be a viable project for one person may be entirely unsuitable for another.
Your research idea needs to be of interest to other academics in the field. Partly, this will depend on your ability to justify your research and the originality of your proposal, but it can also depend on timing, as technology makes new things possible and old
techniques obsolete, and as various theories and areas of study come in and out of fashion.
The interestingness of your project to others depends on who your audience is, as some projects will be fascinating to some, utterly pointless – or in some cases even offensive – to others. This is worth bearing in mind not only when you present your
complete research for examination or publication and nominate examiners or referees, but also when you choose whom to work with; if your supervisor is fundamentally opposed to your project, then you should either choose another project or change
Although a degree of originality is a key requirement, research is never totally original. Rather, it operates on the edge of what is already known; venturing forward but still connected to and dependent on that which has been done before.
Not every aspect of your research needs to be original. The skilful application of unoriginal ideas and well-established techniques gives you a reliable foundation to work from, and even the most revolutionary research will rely upon much which is unoriginal, perhaps combining pre-existing elements from disparate fields in an original way.
Find an edge to work on
Academic research is analogous to learning, but on a societal scale. Just as when learning a skill, research pushes just beyond the edge of society’s current collective ability or knowledge.
Rather than searching for a gap where there is nothing, it may be better to search for an edge to work on where you can take existing research further. One way to do this is to ask yourself after reading a paper: “is there a way to expand upon this research, or to approach it in a different way, or to apply the same techniques to a different subject?” If you do this with several papers, you’ll find that there is no shortage of ideas.
Another approach is to test the basic assumptions that others in the field have used. It is quite possible for an assumption to become accepted fact simply because several authors have stated or cited the same idea, even though it has never been systematically tested or proven. If you find such an untested assumption and can think of a way to test it, then your work will be of great value to the field (provided it is well executed).
Developing an idea
The decisions you make early in your PhD about what research to pursue will affect everything that follows, and this puts a lot of pressure on your choice of project.
Creative processes tend to work best when you take the pressure off and allow yourself the freedom to consider many ideas without worrying about whether or not they are good. This freedom is important because, often, bad ideas serve as intermediate stages in the development of good ones. So allow your imagination to run free, think of many ideas and don’t worry initially about finding the one.
Developing an idea is not just about freedom of creativity though. Once you have a few ideas it then takes focused work to test their viability and to refine them into a potential research project. How, then, do you test viability?
You will certainly need to check the existing literature to find out whether your idea has already been investigated and what similar research has been done. This is partly to ensure that your idea is original, and partly to help you think through how you might conduct your own research.
The literature can show you how other researchers have approached similar problems, but it is also useful to talk to other researchers in your department; to get feedback on your ideas and to find out what resources and expertise are available to you.
Even if you are given a specific problem to work on there will be multiple possible ways to approach it, so it’s good to think through these alternatives, consider their practicality, and not necessarily just take the first option that comes to mind.
Developing a research idea means investing time and energy into some ideas that you don’t then pursue further. This is not wasted time—it is often through investigating a bad idea that you then develop a good one.
Sooner or later though, you will have to commit to a project. There is no set formula to follow here, but there are some questions you can ask yourself, which may help you decide.
- Does the project have a clear aim?
- Do you know what techniques you will apply?
- What resources and funding will you need?
- What skills will you need to develop?
- Do others in your department have relevant expertise?
- Are you interested in the project?
- Can you justify why the project should be of interest to others?
- And who will it be of interest to?
The natural temptation might be to set your aims as high as possible and make your project as comprehensive as you can. Such projects are easy to imagine, but much harder to implement.
Think of the simplest possible version of your project, and how you would go about it. Then you can add extra complexity, but bear in mind that you will have to achieve the simple version first.
A word of caution
Although it is good to choose a project you have some interest in, it’s possible to be a little too interested in the subject. Using research to prove something you passionately believe in can lead to confirmation bias, where you only pay attention to results that support your existing view.
It’s OK to expect a certain result, but as a researcher you should maintain a slight distrust of your own assumptions, and actively try to prove yourself wrong whenever a new result conforms to your expectations.
Depending on your PhD programme, you may have to write a research proposal. The requirements for this differ between institutions—you may have to write the proposal before being accepted as a student, or it may happen at a much later stage. It’s up to you to find out how it works wherever you are. Generally though, your proposal will need to show a clear research objective and choice of an appropriate methodology.
Clarity is the key. It should be immediately obvious exactly what you are trying to do, and this is only possible to communicate if you first have clarity in your own mind. Do not attempt to write down everything you could possibly imagine doing, nor everything you know about the subject.
Get the book
“PhD: an uncommon guide to research, writing & PhD life” is now available via amazon and other retailers