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One of my close relatives went to Australia to get a Ph.D. in computer science. PhDs in Australia are 3 years long. She couldn't complete her Ph.D. in 3 years. Then she applied for an extension and got 1 year more. However, ultimately she failed. I asked her about the issue and she preferred to stay silent.

As far as I guess, she chose a topic that was destined for failure. I.e. her hypothesis was incorrect.

How should someone choose a Ph.D. topic so that she doesn't fail?

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    Failing the PhD because the topic was destined to failure is an advisor's failure.
    – Massimo Ortolano
    Oct 11 '20 at 7:55
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    A failing hypothesis is not an ultimate reason for a Phd failure. Sure, papers on a hypothesis that proves to be false are harder to publish, but a Phds purpose is to certify that you can do sound scientific research. Proving that something plausible is not true is part of that. So while a failing hypothesis can be a hindrance it is not sufficient to cause failure in a Phd. Oct 11 '20 at 15:39
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    If you could predict "success" in "proving" an hypothesis three years in advance, you wouldn't be doing research. Research is exploring the unknown, not giving reasons for things known to be true. Alternatively, you would be doing some trivial exercise, going through motions to no useful end.
    – Buffy
    Oct 11 '20 at 15:45
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    I'm not sure if any of my Aussie PhD friends finished within 3 years, and even taking longer than 4 years is very common. Did they actually fail, or have they just run out of funding? Do they need more funding? Is it now just time to finish writing up what they did? Oct 12 '20 at 4:52
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    This whole question seems very strange — the asker’s assumptions are wrong, and their motivation is unclear. It’s like asking “My friend got married, but then got divorced. I presume this is because her spouse was a bad cook. How do you make sure that your spouse is a good cook?” Sure, we can answer the specific question — “Have them cook for you earlier in the relationship.” — but is that really what you wanted to know, or was it “how can I make sure that my marriage will be good”, or “how can I tell my friend what she should have done differently”, or something else?
    – PLL
    Oct 12 '20 at 12:00
46

Make sure your advisor has a good track record of graduating students in time.

Anyone just entering or outside the field won't be able to assess PhD topics with good judgement, so it's unfair when advisors fail their students by giving them bad projects. Your best bet at avoiding this is finding an advisor who is unlikely to fail students in this way.

If you find yourself in this position, a good bet is to reach out to other professors and tell them what's going on. It can feel shameful, but I've seen many success stories of people getting a new project and spinning it into enough for a PhD when things aren't working out with their initial advisor.

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    we do not know that the cases of the OP was that the project was bad.
    – lalala
    Oct 11 '20 at 15:22
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    @lalala OP literally asked the question of how to avoid choosing a bad project. I never weighed in on the hypothesis about OPs relative, I just answered the question OP posed.
    – Well...
    Oct 12 '20 at 5:59
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    This is it, choose your supervisor not your subject. A good research subject will be trashed by a poor advisor, and in any case your approach will be completely dominated by them. Look at what happened to their previous PhDs including their initial years post-doctorate, because they too are typically dominated by the PhD and supervisor. Younger supervisors are more cutting edge, driven and empathetic (by temporal proximity) to the PhD's situation. Older supervisors are more experienced and connected/senior in their field. Either kind may be abusive or destructive because academia allows though
    – benxyzzy
    Oct 13 '20 at 6:30
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    Yes, the advisor's track record is the dominant feature. Sure, other things have some effect... but nothing else as much as this. Oct 13 '20 at 17:42
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A PhD is awarded following submission of a thesis. It is extremely rare for a student who submits a thesis to fail. It is quite common for a student to never submit a thesis.

If the goal is simply to pass, then the key questions should be:

  • What are the expectations for a thesis in my discipline? Expectations vary, but usually originality is expected.
  • Will this thesis topic allow me to meet those expectations?

The one situation where a choice of topic would be likely to directly cause failure would be if the topic is blatantly not original. For example, it is found in well-known textbooks. It is much more common for a student to stop working on their thesis because they do not like the topic.

Financial and health factors are common causes of PhD non-completion.

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    usually originality is expected? There are exceptions to that? 8-(
    – einpoklum
    Oct 12 '20 at 8:12
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    There are absolutely thesis topics with little failure potential. These are usually also recognizable from afar for anyone in the scientific community, so they are mostly useful if you need an academic title for political reasons but have no other academic interest. Oct 12 '20 at 17:00
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Speaking as someone currently in the trenches, I’d advise the following general strategies for a doctoral student to maximize their chance for completion. At the very least, all these points should be considered. Also, as others have said, you won't fail a dissertation for having a hypothesis that yields a negative result – a dissertation is very much about the process not the scientific result per se.

  • Develop your dissertation to play largely to your strengths, not address your weaknesses. For example, if you’re really strong at biological research but have only just learnt to code, it might not be a good idea to have a dissertation that is centered on building a software platform – even if it does target biological research as its domain.
  • Choose a topic for which you’ll have expert guidance. That means your advisor and members of your committee can understand the concepts, methodology, and novelty of your work. Their advice will also be that much more helpful; they’ll be better equipped to help you navigate the roadblocks that’ll inevitably crop up.
  • Do the background to make sure you’re addressing a real gap in the current literature. It pays to be a bit future thinking and aspirational; as a PhD student, one of the advantages you have is a multi-year timeframe where you can largely focus on one thing. Don't be afraid to think big and then narrow down your focus – doing so can help give you a larger sense of purpose; it can help you remember how the little thing you're working on in the moment factor into your larger vision.
  • Discretize and make independent the goals of your project. This can be tough to do, but it’s a highly effective strategy and can ensure some degree of impact among your final research products. If each goal builds on the other, it's easy for your entire project to hit a roadblock after you've already invested a lot of time into it, which amplifies the risk that your entire project could fail.
  • Be wary of situations and research designs that will precipitate bureaucratic delays. IRBs, data access committees, awaiting approval from distant stakeholders (timezone delays can add up!), and long duration data generation are examples of this. If at all possible, design your project to at least have a primary endpoint that won’t require more than one of these. Note that not all of these potential roadblocks are created equal. In my experience, the order of the above delays looks something like this: Long duration data generation > IRB > data access committees > distant stakeholders.
  • Document communications and decisions with your committee and administration in writing. For example, when seeking input on a larger project decision from your committee members via email, be sure to state (in a friendly way) when you need a response by and the default action that will occur if no response is received by that date. Send a friendly reminder 48 hours before the date if you haven't received a response. For big decisions and reviews, allow your committee 2 weeks of lead time.
  • Have an insurance policy. This is something I often setup before making a big career decision – ultimately, failure is always a possibility. What I mean by this is to have something to fallback on if your primary focus (i.e. your doctorate) ends in failure. As an example, I completed an MS prior to pursuing a doctorate and have a software side project and associated business plan that I believe are together legitimately valuable and actionable – at the very least, both would help me land a job that I would enjoy and keep me stable. Having 'insurance' can help give you peace of mind and sustained focus when pursuing something that might be inherently risky, and in some respects doctoral degrees are.

This isn't an exhaustive list; there are other considerations as discussed in other answers. That said, in my personal experience (and observing others at my institution) I’d recommend being mindful and discussing all of these aspects of your dissertation, possibly throughout your doctoral research, with your advisor and/or committee, though the latter may be best discussed with your peers.

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    "Go big" is a very dangerous suggestion -- it's very easy to overdo it and end up with something that is not realistically doable on a ph.d. timeframe. Again having the guidance of an advisor is of course crucial. Oct 11 '20 at 17:43
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    "Scooped" isn't really relevant for a thesis. For a paper yes, but no committee would fail you because someone published something similar or the same. The point is you put in the work, got the result, and wrote it up in good faith. Oct 11 '20 at 23:07
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    @DenisNardin I agree – I misspoke, I've updated my answer to better communicate what I inteneded.
    – Greenstick
    Oct 12 '20 at 0:06
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    True - just clarifying because the title question was about dissertations, specifically. Oct 12 '20 at 0:20
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    Many of these are great suggestions for research in general and could also benefit postdocs and early career professors. Oct 12 '20 at 15:43
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It is an empirical fact that the percentage of graduate students who fail to complete their PhDs is quite high.

It follows that there does not exist a simple algorithm for choosing your PhD topic that guarantees success - certainly not one that fits in the space of an academia.se answer. If it did exist, everyone would know it, and we wouldn’t see the numbers of people who start a PhD and don’t finish it that we do end up seeing.

Finishing a PhD is a matter of talent, a lot of hard work, and in some cases a bit of luck. It’s good to do some advance research on best practices for choosing an advisor and a topic, but no amount of preparation can save you the need to have some combination of those three things.

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    Do you have any statistics for the high rate of PhD dropout? In my experience, everyone I've known who started has completed, so that is quite surprising to me. But I do say this from the point of view of a student, rather than faculty.
    – Phill
    Oct 13 '20 at 4:11
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    @Phill I don’t have statistics, sorry.
    – Dan Romik
    Oct 13 '20 at 5:11
  • In all the grad math programs I've seen in the U.S., less than 10% of students do not complete their PhD, and most often they discover within a year or two of beginning that they don't want to do math... not that there's some obstacle otherwise. Oct 21 '20 at 0:07
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I want to reassure you that don't fail a PhD dissertation because your hypothesis was incorrect. If you are stressed about this on your own behalf- don't be. Your result is outside of your control.

To reassure you, null results are published all the time. For example, "The Ineffectiveness of using Generic Deep Learning approaches on Problems of Type XYZ" can be published in a great journal, so long as your readers still learn something important from your article. Here's what reviewers look for, in general:

  1. The methodology was sound.
  2. The argument that one could have expected your approach to work was clear and agreeable to your audience.
  3. The paper was well written and clearly outlays the conclusions and implications for the field that practitioners care about.

Having an interesting and successful thesis helps, no doubt, but it is not the sole issue here. The demands of 1,2,3 are very high.

That said, if your friend doesn't want to discuss why they did not complete their PhD, I would avoid poking at them. There are innumerable reasons why they might not have finished it, and it's best not to speculate. You may easily arrive at an incorrect conclusion. Heck, perhaps they dropped out because they got a great job offer as ABD.

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As far as I guess, she chose a topic that was destined for failure. I.e. her hypothesis was incorrect. How should someone choose a Ph.D. topic so that she doesn't fail?

I think your hypothesis here might be incorrect. You could in theory write an entire PhD thesis based on an incorrect hypothesis. The entire point of the thesis would become disproving the hypothesis.

It's obviously not as satisfying as proving something is true, but it's valid science. If the original hypothesis was reasonably plausible, it means others won't have to repeat your mistakes.

And in any case, the point of a PhD is not so much to produce useful new science, as to produce a new scientist. I.e. someone who can demonstrate, through their thesis, that they understand the scientific process well enough to produce original results. It doesn't really matter, that most of the time, these original results are pretty useless! The originality is just a way to prove that the science came from them, and not someone else. It's only purpose is to demonstrate the following hypothesis: "Dr X is, indeed, a scientist"

Possible reasons for failure:

  • lack of support from the advisor (a good advisor would advise how to turn that failing hypothesis into a successful thesis)
  • mental breakdown of the student (it can be soul-crushing to spend so much time trying to get something to work, and failing)
  • lack of time (if the people involved realise too late that "this isn't working", and lack the "narrative" skills to quickly turn that apparent failure into a success)

Note: people doing research in computer science can get a bit confused about what they are actually doing. Science is about asking questions, finding answers, and writing about them. So it can't really "not work". A negative result is still a result (unless you entire experimental set up got destroyed and your data corrupted, as long as you follow proper methods, you can't really fail) However, engineering would be about using science to produce a workable solution to a problem. Now this can very much fail. This is not what a PhD is about. But people can get misguided. Computer scientists ("I must write about computer science") who think that what they're doing is software engineering ("I must deliver working software"), are very much at risk of failing. And sometimes the way a PhD thesis is funded (e.g. industry grant) can fuel that misconception.

Note 2: re "originality", a very plausible cause of failure, is if you start your PhD on a valid original topic, but then someone else basically writes your thesis before you've finished it. This happens all the time... And is incredibly stressful/frustrating! Same problem with publishing papers. Some topics are popular, and great minds think alike... So it's really not that unusual for different people to be unknowingly working on the same hypothesis in parallel! And I honestly don't know what's the best way to avoid that situation, and to salvage your hard work, when someone else beats you to the finish line... (I guess try and publish anyway, even if originality takes a hit... E.g. introduce a small variation, etc. But all the extra testing and writing can really screw things up in term of timing, when grants are running out)

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When one fails or is about to fail a Ph.D., it is worth understanding what requirements are not fulfilled. This may vary from a field to field but generally, there are four sets of requirements:

  1. Formal criteria required by law. These are usually vague and the easiest to fulfill. They dictate the number of course points, seminars, and some generic requirements like "contribution to knowledge" etc. you have to fulfill to get a Ph.D.

  2. Requirements by the university. These may specify the thesis format, specific courses to attend, teaching work, funding, etc.

  3. Requirements by the community determine the level of quality that is considered good and worthy of publication by other researchers in the field.

  4. Requirements by your supervisor. These are tricky because they are implicit. Inadvertently, you may get a very demanding or difficult supervisor, or, alternatively, you can have a very supportive one.

The exact thesis topic is largely irrelevant. As long as it broadly falls within CS (or any other study area) you are fine.

What matters is that a student knows the formal criteria. There should be quarterly/yearly evaluations and the supervisor/university should facilitate the student in attaining them.

Having publications of thesis work is a good sign that the work is of reasonable quality. Maintaining a good relationship with the supervisor help with understanding his/her expectations.

From my anecdotal and very limited experience, students fail PhDs for two reasons:

  1. Difficult relationship with the supervisor due to misunderstood expectations, mismatch of personalities, inability to receive critical feedback, unwillingness to put in hard work, leading to..

  2. Difficulties in publishing their results either due to preparing manuscripts taking forever or being repeatedly rejected from peer-reviewed venues. Lack of progress exacerbates #1

To conclude, the advice to anyone starting a PhD is to pick the supervisor carefully.

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I am a professor, I have been on more than 20 doctoral committees. Most of the answers here are focused on, or call attention to picking a topic. IMHO - by itself this is not a good strategy.

In my experience, all dissertation decisions hang on one thing: the candidate's ability to understand how gatekeeping works. That is to say the classic error is the doc candidate who thinks they want their work to be great so they find the smartest people on campus to be on their committee. Translation: the four biggest egos in that discipline on campus are now on your committee. Good luck with that. Applying such a belief system (get the best and brightest) has the potential to inspire Intra-committee disagreements. That's risky. The worse-case output is the dissertation never gets done and it's not the candidate's fault.

IMHO if you want to create the most favorable conditions for graduating, research your potential committee chairs. 1) are they well-liked, respected? 2) research potential chair's doctoral committee history and records of how many successful/not successful dissertations 3) information interview your potential chair. 4) once chosen, ask your committee chair who should be on the committee.

The chair will likely recommend people who are agreeable with their ideas. Your committee meetings will be friendly. Don't get me wrong, you still have to find a good topic, be clever, and write well. A good advisor will steer you away from rough seas, heal weaknesses in your work, or advise strategies to keep your work relevant. IF you don't have that in your corner, you can still finish, it's just a lot more work to figure that stuff out on your own.

IMHO when it comes to topic and writing, buy or otherwise acquire a doctoral candidate or 'dissertation' handbook. Most universities have them in some form, usually found at the department level. Get one, read it, follow the guidelines laid out by your department -- and keep a journal of your committee meetings. Where you can, use the rules (and your notes) to your advantage.

The bottom line is that earning a phd requires you to pass through an institutionalized system. Such systems have rules and structures that can be learned and used to create pathways to success.

My experience on doctoral committees -- 20% of the dissertation ideas are not (and never will be) well conceived, 20% are exciting and interesting, The middle 60% are well-written -- or technically well-executed (and not so well-written), but otherwise good. Prolly 10% of candidates are rejected, and we always attempt to counsel our candidates to bail out early if we think they won't make it.

Good luck with your ambition. It's worth the effort. I was 20 years owner of a software company, now 20 years as professor.

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My answer is basically for US as that's where I am from, and also where I got my Ph.D.

Advisor is key. Work with your advisor to pick an approved topic. The advisor will typically know what will work.

It is important that the PhD candidate's research have original research, but it also needs to be related to and compared to past research, so extending past research is important. For example, creating a new algorithm would obviously be original research. Finding statistical equations for existing algorithms would be extending past research.

It also helps to finish the work in a timely manner. Most PhD candidates have done enough reading, so it cannot be emphasized enough to write up the research. If it is possible to publish it or present it in a conference (these days, likely to be a virtual conference), this will also help.

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