Is it feasible to take an unsure PhD topic?

Question

I was working towards converting to a PhD but was unsure of what research I would do. Suddenly an idea striked my mind and I discussed it with my advisor. He doesn't have much experience in that exact field but has been in the area for around 6 months.

He said that he thinks that idea is feasible but doesn't know what would be the approach, and not sure whether the results would be positive in terms of PhD because there several parallel domains. Moreover, literature doesn't have much details on that exact topic. And my literature survey (pretty limited though) has only enhanced my confusion. Probably because my idea deals with application of a recent class of techniques to optimize a problem.

Is it worth to convert to a PhD with such an idea ?

Answer 1

This is exactly how most of the really great PhD students I've seen have all started. Working on a problem with unknowns is a process called "research."

Clearly, you are going to have to find some collaborators with more experience in the field than your advisor, but that's part of the process as well. Hopefully, your advisor can assist with networking / introductions / etc. The support of your advisor will be critical (as it is for all PhD students).

The trick is to make sure you have a backup plan and a way to convert to it if necessary. Don't spend three years mucking around if you're not making progress. But, spending 6 months investigating if there is something there -- that's well worth it.

Answer 2

Not sure there's a correct answer here, but I would recommend against it. The goal of your PhD research is twofold:

1. Introduce you to the world of Academia
2. Earn you a PhD

By choosing your topic to be something completely exploratory, you put (2) at risk; the research may not pan out, or may be much more difficult than you think, or may be infeasible for technical reasons, or whatever, and your PhD would be at risk.

However, to reiterate, this is a function of the specific topic at hand, your risk appetite, your advisor's skillset and risk appetite, and your willingness to restart your research partway through your program. Take all that into account when making your decision.

Answer 3

I like eykanal's answer, and I would add this: I know many people who changed the topic after one year of their thesis, and if they put enough effort into it, they still finished in time (being <4 years here).

What I mean, if you start working on one problem and you finish solving another one, you still can graduate and get your PhD. However, depending on your subject, this might be more difficult: for us "theoreticians" who work in an office it's simple, for people who do complicated experiments it's of course much more difficult or even impossible.

Answer 4

While research is inherently risky, there are two red flags:

He said that he thinks that idea is feasible but doesn't know what would be the approach, and not sure whether the results would be positive in terms of PhD because there several parallel domains.

What this tells me is that your advisor does not have the specialization to attack this particular idea that you are proposing; moreover, there are other areas of research that may be examining the problem that you are discussing.

There are a number of potential issues that come across from this:

1. You don't have an advisor who's familiar with the area, so you have to spend more time (either doing your own related work, or finding other faculty/collaborators) to discover the appropriate methods. Instead of having your advisor go, "Use this equipment and this research method", now you have to possibly discover what the method is and then acquire equipment for it. You will make mistakes numerous times because no one is there to help you avoid common mistakes. This makes your results take longer and uses more money.

2. If there are parallel domains, then there is a risk that the results that you and your advisor find from the work (that most likely took a long time because people are unfamiliar with the method) are possibly not as significant or as important as they first seem because this other area's already identified them first. Others familiar with the area might ask, "Why didn't you look at XYZ and ABC first?" and reject the paper. As a result, it will take additionally more time to familiarize yourself with these parallel domains in order to identify that what you're doing is important, relevant, and novel.

I think personally that (1) is a much greater risk than (2). Most people never come into an area with knowledge of what's there, so surveying related work, talking to people, and learning about the research area is usually work that has to be done anyway, but (1) can be very deadly. (1) and (2) in combination can be very dangerous, since it might indicate that your advisor simply doesn't have a lot of interest in Method (1) and in Result (2) - which means that your project might end up with less priority, less input, and less money. And all of that results in less papers and less impact.

Less papers, less impact means less opportunity to do important, meaningful work (and fewer job opportunities).

Thus, it does depend partly on what your personal goals are. If you do want to pursue this path for the sake of expanding your knowledge and the knowledge of the world at large, then one possibility would be to switch advisors or to find out who's doing this work in parallel domains and collaborate closely with one of these other researchers so you can get technical knowledge from those people.

Answer 5

Converting to PhD should not be dependent on an idea, I think.

If you want to do PhD then go for it. If one idea does not work other will. That's what research is all about.

Apart from taking up that idea further:

1. Your supervisor does not have enough experience in that field that means you are entering at your own risk.
2. Do a good 2-3 months detailed literature survey to understand it better and then take a call.