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I'm a first year PhD student. I'm just reading background papers trying to find a topic for my thesis: my subject is turning around tree different elements (XML (as a tool), complex data, and the cloud computing (as an environment)). So I find that is a large subject with many materials that treat this subject, whether each element individually, or two elements at most at a time, but not all three together.

My question is

How should I choose the most worthy materials so that I could find a good topic which uses these three elements together?

Any information, insights, or propositions are welcome. Thank you.

  • I cannot imagine a strong Ph.D. thesis about XML. – user14102 Apr 19 '14 at 22:41
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Find out what the most current problems in these fields are. This can be done by reading papers in the most recent proceedings of the conferences and journals dedicated to these topics.

Regarding these three topics:

  • XML is, as you say, a tool. XML in itself is not particularly novel and a lot of research involving XML is of the form "Something interesting and known in XML." I find such papers unexciting and reject them if they pass my way.
  • Cloud computing is a hot topic and there will be lots of people working on it. This means that it is easy to find papers and easy to find a venue for publications. On the other hand, there is a lot of competition.
  • Complex data is and will always be interesting. But what do you plan to do with it? Are you planning to use the cloud to process massive amounts of complex data? That is certainly a hot topic these days, with things like Google's Map-Reduce framework and other comparable things (Hadoop, Cassandra, ...). A lot of big companies have interest in such settings, so it might be challenging to find something new to do, but you will likely have people interested in the work you do.

In short, I think you only really need to consider the complex data and cloud computing combination. This will make your search a little easier. Then find the top conferences in the area and read the proceedings from the last few years.

In addition, it is crucial that you build on top of what other people have done, rather than starting from scratch. Ideally, start with something developed by people in your own lab (whether it be a system or a theory).

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I can answer this from the perspective of someone who did it poorly in retrospect, but from a different field (engineering). You will want to make sure that any papers you begin with are:

  1. Accepted findings in the field. I made the mistake of basing much of my thesis work on a paper which was used a one-off paradigm, and was not replicated by anyone other than myself. This resulted in my needing to spend much more time validating my results than I otherwise would have needed to, because there was no other validation in the literature.

  2. Simplicity over novelty. You're a graduate student, at the beginning of your career. You'll have tons of time to do awesome things as your career progresses. Unless you're working for Dr. Awesome BigName Researcher whose lab is known for doing cutting-edge work on X, be conservative... choose the less exciting but more likely to work research over the more exciting but very complex and/or more likely to fail.

Note that this post is completely irrelevant to anyone whose advisor effectively tells them what their thesis project is, as your criterion will be (1) the papers your advisor hands you. You have my sympathies :)

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  • Why would the outcome affect the study? After listening to a recent Planet Money podcast on "The Experiment Experiment" (sic), I'm curious why the probability of a success/fail should lead to any decisions. Shouldn't the process and discovery be the important thing, regardless of outcome? – vol7ron Mar 24 '18 at 15:56
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I think the answer to your question depends on the aims you want to pursue with your thesis.

  • Start a career in academia. In this case I agree with eykanal. Use something that enables you to build a solid foundation.
  • Start a career in industry. Look at the particular industry/company you're interested in and decide what's going to be most important to them and hence most important in facilitating you getting a job there.
  • Neither of the above. If you don't really know what you want to do after you've finished your PhD, I'd say go for the thing that interests you most, even if the results you're basing your research on is novel and you're not sure if it's the right direction to go in. That's why it's called research after all :)

In any case you should make sure that you're comfortable doing the research. The best papers are no good for you if there's no scope for you to extend the work or you can't build on it for other reasons.

In your particular situtation I would probably focus on papers that bring the different subjects you've mentioned together, as this gives you the option of shifting the focus of your PhD slightly in one direction later.

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  • Thank you Lars Kotthoff, your advises are very valuables, that's really what I wanted, I'll absolutely consider them. – Nafaa Boutefer Mar 6 '12 at 7:31
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    The advice that I received, and that turned out to be correct in my case: for a career in the industry, it is irrelevant what the thesis is about (at least -- in my case -- for the field of Mathematics, and for the software development industry). The fact that it is a Ph.D. from a decent school is all that matters. – user14102 Apr 19 '14 at 22:39
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One point not covered by the other answers is Review articles which summarize the state of a particular research field.

As the OP is at an early stage of the process, these are especially useful for gving an overview of the most important work, and are usually written by an authority on the topic. They can be invaluable in preparing a reading list, as the references are the ones that are considered central to the development of the field, and will often be articles that you'll be expected to know.

Even when looking for inter-disciplinary stuff it is usually useful to begin with review articles from all the sub-fields that touch upon the research topic. The Annual Reviews series of journals are a good generic place to start, though you should focus on the leading journals of your field. The number of citations that can be checked on google scholar are also useful in establishing the important research concerns of your field to know before you start working on something brilliant that nobody will care about. For instance, there might be excellent reasons why nobody has done work usng your chosen approach, so getting the most respected/ cited papers will help you identify useful research topics, and also the ones to avoid.

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