Is it okay if research problem is vague in the initial phase of research?

Question

In short, I am a Ph.D. student computer science ( theory ) currently in the mid-stage. I have one serious doubt about the research process. I have worked on just two problems in the past and from that experience, I have felt that the research problem in the initial phase of research will be vague ( means research problem will be broader and somewhat less clear ) and as we start working on the problem, it will become clear and many times we will change the even original research problem. In the end, we will think about what results, we have and on the basis of those results, we will again change the research problem ( if needed ). There are a few problems with the above research process

1. Takes More time
2. More frustrations etc

Is the research process will be the same even after my PhD, I mean or I will become more careful with time which may lead to giving me a better way to do research.

Question : Is it okay if research problem is vague in the initial phase of research?

Answer 1

In my opinion this is the definition of "research" everything else is "development". Of course, from "devlopment", serious research questions may be derived.

In my personal opinion, a PhD work whose proposed result is known from the beginning is worthless.

It's a different story if the problem is too large for one person or maybe not solvable at all - then it needs to be re-adjusted based on the experience made so far. But this process can / shall be part of the PhD!

Answer 2

From my humble experience, and for you question:

Is the research process will be the same even after my PhD

My answer is No. In my case, there is no comparison between my first research and even the second one. The more I acquire knowledge, the more I become experienced in identifying research gaps and asking the right questions from the first place. I also become able to think of what it takes to implement/do the work needed. The reviews I got from the first two papers taught me a lot on how to present my results and what are the key points that are needed to make my results presentation (in the papers) sound.

I confirm again that in my case, things get easier and clearer with time.

Answer 3

For a PhD candidate, a vague research topic has an additional risk. It is possible that nothing sufficient for a thesis will come out of it. Or that anything that might have been sufficient has already been done, published, and mined out.

For a researcher with a significant academic career already established, this is less of a problem. If a prof starts to work on a topic and finds it a dead end, they can usually get over it. Especially since a prof doing active research usually has more than one line of research on the go. Especially when they have several grad students, maybe a post-doc or a research associate. If topic-x fails, then topic-y and topic-z are likely to produce some publishable results.

For a PhD candidate, a dead end research topic could be very much more of a problem. Especially when universities have schedules for how long you are supposed to be working on the thesis. If you spend 2 years and decide the topic is a waste, you have dug rather a deep hole. Possibly you can recover. Maybe not.

Also, it does not need to be a dead end to be a problem for a PhD candidate. If it turns out that there is interesting research there, but that it will take much too long for a PhD, that could be a killer also. Imagine you were exploring the idea of 3-D virtual reality programs, but it was 1970 when computing power was not available to accomplish it at anything like a reasonable cost.

It is a balancing act, and not an easy one. A narrowly defined research subject is likely to be boring, and possibly not publishable either. And even if it is publishable, maybe nobody cares and you wind up with not much of a thesis.

Answer 4

Is it okay if research problem is vague in the initial phase of research?

Ultimately, the research you produce in your candidature should add some original work to the discipline, and it will need to be sufficiently specific that you can subject it to peer review and publish it in a scholarly journal. It is not unusual for research investigations to begin at a "vague" level, and then progress to the point where specific research questions of interest emerge and are solidified. In a PhD program, there is a rule-of-thumb that the first year is often spent finding a broad research field and formulating ideas, and then by mid-stage you should have progressed to the point where you have specific research questions and you are now able to make progress towards publishable work. If you are mid-stage, but are still at a "vague" level of analysis, you might be a bit behind schedule, but there are plenty of PhD candidates in that boat. You should check your progress with your supervisor and formulate a plan for progression.

In order to progress your research, sit down with your supervisor and hash out some ideas for possible research topics/questions within the broad field of interest to you, and make some proposals for specific research questions you could study within this broad research problem. If the broader question is too large and complex for a single project, see if you can formulate some narrower questions to start an analysis in that field, so that you can formulate a specific PhD research project. Try to come up with an idea for a preliminary paper, and this research paper will naturally lead you to ideas for extensions. Since you have not described your research problem, there is no basis to speculate on whether your "vague" research idea is likely to crystallise into publishable work that is suitable as output from a PhD candidature. As with any other research problem, you should seek guidance from you supervisor on this.

Although I cannot speculate on the value of your "vague" research problem, it might be helpful here to mention an analogy to this issue that arises in my own research field (statistics). In statistical work, there is a distinction drawn between 'exploratory analysis' and 'confirmatory analysis'. In the former, we use data to explore and describe general patterns that give rise to broad hypotheses of interest, for future testing. In the latter, we formulate specific hypotheses that are ready for statistical testing, and we use data to test those hypotheses and report the results. Both of these activities are legitimate avenues of research, and both can lead to published work. (It is more common to see published statistical work that performs confirmatory tests, but a good exploratory analysis is also valuable.) Depending on your specific project, there may be analogous research projects that you can pursue in your field ---i.e., projects that explore a problem, present some exploratory analysis, and offer hypotheses and theories (without necessarily testing them), and projects that formulate a specific testable problem and make progress on that problem.

Is the research process will be the same even after my PhD, I mean or I will become more careful with time which may lead to giving me a better way to do research.

The more you practice something the better you get at it. If you complete your PhD and become a researcher then you will find that you gradually get better at assessing a potential project for possible research outputs, formulating research questions, and producing publishable research. Everyone starts off bad at this, and even the best PhD candidates are nowhere near as proficient at these things as professional researchers. Like any profession, you start off with few skills, and you gradually get better with practice. The PhD candidature is like an apprenticeship; it takes in novices and tries to get them to the point where they can conduct independent research. Seek assistance and advice from your supervisor as often as needed, and assess your progress relative to your status as a novice researcher.

In regard to this issue, it is worth noting that it is extremely common for PhD candidates to overestimate the amount that can be accomplished in their candidature, and assess their abilities and progress pessimistically, relative to unrealistic expectations. Your goal as a PhD candidate should be to produce some publishable research, while noting that it is usual for research published at this stage to give some modest gains in the field. If you can publish a few papers that make initial in-roads into a research problem then you will have done well. If you later complete your PhD and become a researcher then you will have plenty of opportunities to research your field more deeply.