Do PhD students sometimes abandon their original research idea? If so, how do they cope with it?

Question

This might be a silly question to ask, but I initially had a great research ideas in mind during the early part of my PhD program but due to the unexpected circumstances I now think that I have to abandon them and start searching for new ideas from scratch (2 of my ideas were taken by other researchers in my field recently and I don't think I have capability to work on my other idea), which I find really depressing.

Does this normally happen for PhD students? If so, how do they cope with it? Do they just start all over again from the literature search and brainstorm for ideas?

Thank you,

Answer 1

Not only does this happen frequently to PhD students, it also happens occasionally to experienced researchers. Many research projects are embarked upon in a somewhat speculative manner, where we do not really know what the answer to a question will look like until we get there. Sometimes we get stuck and cannot get the answer to our research question, sometimes we get the answer but it is so trivial that we realise we were thinking about the scope of the problem incorrectly, and sometimes we get the answer and we then find out that others have already figured out and published the same answer before us (which is something that does not always show up in your initial literature review).

It is less common for experienced researchers to completely abandon projects, because we have pretty good a priori judgement of what will work, and we are also good at salvaging work if it does not turn out as planned. Moreover, many academics tend to put unsuccessful projects "on hold" and come back and think about them periodically to see if they can be changed in some way to give fruitful research. During my own PhD candidature and my subsequent research career as an academic, I have started and done work on several topics which I have subsequently "put on hold" or altered to such a degree that the initial topic was essentially abandoned. I have had other topics where I did a whole lot of research, even wrote up a paper, and then subsequently found that I had merely rediscovered results that were already in the literature (under a name I was not familiar with). I also have probably ten or twenty started ideas sitting around and stalled because I have encountered some roadblock that may or may not be fatal to the future of the project. As you will see from some examples below, I have had some absolute doozies.

Mine have come about because I did initial literature reviews that were flawed, and I didn't realise that my research ideas were things that were already well-developed in the literature (under technical names I was not familiar with). In terms of how you cope, well, you look at the silver lining --- often these aborted projects show that you are "on the right track" in terms of your ability to come up with interesting ideas, even though these do not pan out into publications. If you are developing projects that are good enough for other researchers to "take them" then that means you are on the right track. (In my case, other researchers were nefarious enough to steal my ideas and complete them decades before I was born!) It is depressing when you think you have a great idea and then it turns out not to lead to anything, but you look on the bright side --- it is better than having no good ideas at all.

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Some (kind of embarrassing) examples from my own research career

Rediscovering the theory of identifiability: When I was in the first year of my PhD in statistics I came across an interesting problem that I thought would be a wonderful PhD topic and I spent many months solving it and writing up an academic paper for a journal. I was extremely happy with my paper and thought it would be a big deal, since it seemed to me that I had developed an important concept that would be a great addition to statistics. A couple of weeks later I got a desk rejection from the journal, and the editor was kind enough to gently inform me that while my paper looked very interesting, and was well written, my ideas "look a lot like the theory of identifiability" (a term I had not heard of at that time). Using this new term I did another quick literature search and discovered a huge literature; my own paper had essentially rediscovered an important mathematical/statistical concept that was already developed and published in about the 1950s-1960s. I had managed to get through my undergraduate degree without hearing this term, and so it had not shown up in my initial literature search, and my supervisors also did not alert me to it when I showed them what I was working on. So, I have the "distinction" of being one of the discoverers of the theory of identifiability (never published), which I discovered about fifty years after its original publication! It was depressing at the time because I had done a lot of work on it, but now I look back and laugh about it.

Rediscovering the theory of constrained optimisation via penalty functions: This one came a bit after I had finished my PhD, when I was an early career academic. I had done a bunch of work on constrained optimisation (Karesh-Kuhn-Tucker method, etc.) and I had thought of an idea of an alternative way of doing constrained optimisation that I thought was novel. Again, I tried searching for it in the literature, but I used the wrong words so it didn't show up. (I think I was calling the method "optimisation via augmentation" which is not its standard name.) I spent my Christmas holidays working on a paper on my method, and was happy with how it developed. When the paper was almost finished, by accident (when looking at another problem) I found a reference to a paper that led me to another paper that alerted me to the literature on optimisation via penalty functions. I had a look at the papers I had found and boom --- another project destroyed. From memory, this stuff was done in about the 1970s, so this time I was a mere forty years late to the party! In this second case I did not submit my (almost finished) paper, so it sits on my computer as a fun little reminder of my Christmas rediscovering penalty function methods.

Answer 2

As a field ecologist, I've seen this happen multiple times. You could imagine any field-based research project is at the mercy of the elements and is often fraught with random variables that might turn out too unwieldy or unpredictable to control for effectively. At best, a field-ecology PhD student may determine after a single field season that the project won't work out (or won't result in easily publishable outcomes) and they switch gears. At worst, this could take multiple years to become apparent (especially if the subject of study takes a long time to grow or the research project relies on periodic or climatic occurrences). I've even seen a student start 4 different projects during one PhD!!

In most cases, I've simply seen the student cope by extending the length of their PhD additional years.

• If the "bad" field season occurs in year 1, then I think a lot of the time no additional length is typically needed, and the student simply changes gears and works efficiently for their remaining 4-5 years.

  • This could involve redesigning the study, "retrying" in the 2nd field season with the new improved design, and working their tail off to finish on time

• If it occurs in year 2, I think there's still usually enough time to jump into another equally-involved project and extend the length of the PhD for another year or two.

• If it happens in years 3-4, I've seen the student shave off a much less interesting aspect of their original question and involve a much simpler sampling design. In fact, I've seen on a handful of occasions where the student scrapped their own field component and simply analyzed available existing data or shifted to more of a metanalysis approach.

  • In doing so, the student still typically adds 1-2 years to their PhD, but they finish in a "reasonable" amount of time (for a field ecologist :p).

In any scenario, especially after a bust field season in year 2 or beyond, I don't think it's too unusual for the student to switch gears to a degree and try piggy-backing on another lab project or extending a previous lab member's work in a novel way. In either case, most of the infrastructure and knowledgebase is available, so they can move on at a more accelerated pace compared to "starting over."

Don't get me wrong: this is a frustrating (and professionally "scary") occurrence for any student or researcher. But take solace in the fact that through the process, most students typically still have completed any necessary coursework, passed qualifying exams, built a committee of (hopefully) useful individuals, and have developed a professional and social circle by the time of their project abandonment. (I hope this can be said of you, too).

• These processes account for a large part of what a graduate student typically needs to accomplish (i.e., they accounts for a lot of the initial time and stress in the early years of a PhD), so having accomplished these "tasks" means that you have additional time and support (not to mention personal knowledge and experience) that you didn't have when you first started the PhD. This means that you can hit the ground running, work efficiently, and hopefully tackle a "new" project much quicker and more effectively than your first abandoned project.

Ultimately, many of us want want our dissertations to be hugely influential or to define us in some significant way so when we leave graduate school we can find that amazing job. This is fair and certainly works for some individuals. However, you, like many of us, will likely still bounce around 1 or more post-docs, assistant professor positions, or industry jobs prior to landing your "dream job." In other words, you've still got time to define yourself and increase your research cred beyond your dissertation. Make the best of the situation, and focus time on forming strong professional relationships through conference meetings, symposia, committees, outreach, etc. Often times having a strong professional network (and demonstrated ability to pick yourself up, work your tail off, and still accomplish a goal) will still help you land a job somewhere.

Answer 3

I'm an early career researcher in my second year of PhD — but by all accounts this is the rule not the exception. I had a strong PhD research proposal which earned me a scholarship (and that I was very attached to) but to my surprise all my supervisors and some other academics really pushed me to explore beyond that idea — ultimately with me developing something far more unique which was only tangentially related to my initial proposal. However, where I landed is far closer to a deeper line of inquiry that ultimately brought me to academia in the first place. In many ways, I'd developed my initial research proposal because I thought it made a "strong research proposal" — but I'd neglected to consider how deeply it engaged me. My supervisors kept questioning "who is this research for?" and "go wild" and offering that the best new knowledge comes from deeper and perhaps more personal lines of inquiry.

Read the literature for inspiration, don't get obsessed looking for "the gap" or you'll never see it. Eureka moments don't occur under duress. Sometimes when you feel like you've been left with nothing, you're in a more optimal position to take more risk. Risk is the most liberating thing for finding new knowledge. Good luck!

Answer 4

This has happened to some friends of mine (in Organic Chemistry) - who had a target of part of a natural product to synthesise, using some novel methodology. Less than 3 months into starting, several papers were published using the same novel methodology on the same products. Fortunately though (despite PhDs being only 3 years in the lab here) this was not such a setback as their PI had other targets and ideas in mind; and they sucessfully defended within 4 years of starting.

Answer 5

I positively invite you to keep track of the development of these ideas as your brainchildren. Please do reflect at a meta level on when, how, and possibly why they came about.

A selection of questions. What made you feel it was worth pursuing them? Which connections did you envisage? Why did the path across the dots appeared self-evident and alluring? Which hypotheses did you test and which not? Which positive/negative state of mind did the situation stimulate? Where did you insist banging your head on in spite of adverse hints? Where did not you crossed an already open door? And so on, and so forth.

Keep a log of your research. Revisit your failures, turn them into the conscious development of your own method of exploring stuff. They are no failures, more a blessing in disguise. Blessings in disguise are seldom time-efficient.

Answer 6

2 of my ideas were taken by other researchers in my field recently and I don't think I have capability to work on my other idea

Please detail what you mean by idea and how much input your supervisor had on what your research plans were. I'm not suggesting you blame your present dilemma on your supervisor - but you must realise that you have to take more charge of the selection decisions yourself from here onwards.

Most theses are loosely defined at first since they will follow a course of their own depending on support expected (but not always delivered) from outside partners and also on the success of your research (not always what we expect - sometimes a dead end).

What most people I know did (and to some extent did myself) was to try and use as much as possible of the work already done, e.g. experimental data, analysis, techniques learned, reading done, perspective adopted, etc., in the new course you chart for the programme.

Talk about ideas for a new (actually amended) programme with others in your research group and with anyone with whom you enjoy a good understanding on life in general.

It's hard to be more precise than this in the absence of what you are actually doing. Buona fortuna.

Answer 7

It is not exactly a rare occurrence but it is certainly a major mistake that could have, may, should have been identified by your advisors. One of the primary roles of an advisor is to ensure that their students are building their doctoral research on a solid foundation. This is a crucial responsibility as the propagation of errors, which could have easily been rectified, resolved, or circumvented with early intervention, can easily undermine years of rigorous and fastidious research and analysis.

Other than a waste of your time and their money, however, the only major consequence is demoralization. The severity of the issue and what it will take to readress the situation to get back on track is hugely dependent upon several factors: the discipline and specific area of research; the proportion of prior research that can be repurposed once you have formulated an alternative focus; how quickly you can rebuild your momentum, but mostly it will depend on your own creativity. I don't think your advisors have served you well up to this point but perhaps they could finally make themselves useful; ask them if you can do a cursory examination of any unpublished data generated by former pupils.

I was very creative and hard working in my PhD program and I used the same approach as I always do in life, which is the three-tier strategy. I had work that was bland and boring but would surely satisfy all the requirements for publication but would require dozens of pages of bullshit jargon to church it up enough for a thesis. I also had a very promising project that was novel, interesting, and had the potential to help a lot of people. The third project was what I played around with on the side, used my own money to fund it, and it was a "Hail Mary" pass; high risk but very high reward.

I realize you've put all your eggs into one basket and your advisors forgot to mention that you can't do a thesis if someone else is already doing it. Perhaps it'll help shift your perspective on how to approach goals, have preformed contingency plans and exit strategies, and how you shouldn't trust the advice, work, data, or conclusions of anyone unless you have personally verified its veracity. If you walk away from this with that paradigm shift then I would suggest that you have learned more in your PhD than most. Good luck, go find some smart creative people in your field and do some brainstorming and you'll be back to the grindstone in no time at all.