How to choose a good BSc or MSc project

Planning stuff...

A critical part of the success or failure of any thesis project is the initial choice of what to work on. This is a surprisingly difficult part of any project, in some ways the most difficult part, and it's something that we see students struggle with year on year. Nothing is so disappointing than marking a project and coming to the realisation that with some better decisions at the beginning of the year a failing project could have passed. This is a trap to avoid, and by avoiding it you will not only improve your chances of passing your project, you will greatly improve your chances of getting a first. In fact, projects are pretty straight forward to do well in, so long as you fully understand what is expected of you. This post takes you through what you need to focus on and avoid right at the start of your project journey.

 

Do something you are interested in

A final year or MSc project is a six month, single person project and in most Universities students will have to study several other modules concurrently. This is a long time to be working on a single piece of coursework, so it is important to choose a project which will hold your attention for that length of time. Moreover, you will be working on other things at the same time, so ideally you need to choose a project that is compelling enough that you want to work on it, in preference to doing other things. 

 

How to know what you are interested in

This might seem like a rather unnecessary topic -- what is "interesting" is very personal and individual. However, estimating what you might find interesting in several months time, when you are under pressure to meet deadlines is not easy. One trick to weight the odds in your favour is to choose a project which you do not, at the start of the project, entirely know how to complete. Like Einstein said: "If we knew what we were doing, it wouldn't be called research". Obviously, don't choose something that is completely outside your area of expertise. If you have spent two years studying bioinformatics then don't suddenly decide to try a dissertation in ceramics, but equally, if you know exactly how to complete every part of the work that you will need to do for your project then your idea is not "big" enough in scope. This point, really is the key to finding a project and much of the rest of this post expands upon it: a thesis or dissertation is not simply a long piece of coursework, it is an individual, self-contained work which should stand on its own. Think of it as a sort of "first job". When you leave University and apply for further study or a job, then the results of your project will be part of the professional portfolio of work you can use to convince a future employer to take you on.

 

Project difficulty: a difficult project is an easy project

By far and away the biggest mistake that we regularly see from students writing project proposals is choosing a project which is far, far too easy. The train of thought seems to go ... projects are difficult, I want to make the project easier, therefore, I will choose a simple idea to work on. The classic examples of this in Computer Science are "a website with a database" -- usually for a family member or friend who runs a small business -- or occasionally a website or database on their own. What's wrong with this? Well... so many things:

1. By the time a student has reached the final year of their degree, they will likely already have written several databases, websites and at least a couple of websites-with-a-database. Therefore, the project is something that the student has already been awarded credit for. This means that the student will not be demonstrating that they can learn independently, and go beyond what has been taught in lectures, which is one of the main purposes of the project.
2. Because the proposal is about the same size and quality as an individual module coursework, it is not large enough in scope to gain many marks.
3. An individual website, in ASP, PHP, or similar, for an SME is a very old problem for which there exist a large number of "turn-key" solutions -- that is, off the shelf products that can be used to create the product. These include templating systems such as Joomla, cloud-based solutions such as Google Sites, Posterous, Tumblr and so on, wikis, and a number of other technologies. A straightforward website-with-a-database is, therefore, in no way a demonstration of the students ability to work at the cutting edge of their field.
4. A website-with-a-database is not a problem, it's a solution to a problem. A project proposal should propose an interesting problem, with a suggested strategy for solving that problem during the progress of the project. 

Having said this, I have seen and indeed supervised a number of excellent projects, for which the student implemented some sort of website and some sort of database. So, it's not that websites or databases are inherently bad choices as solutions to the problems posed by a project proposal, but a proposal MUST overcome the four problems outlined above.

The heading for this section said (rather confusingly) that "a difficult project is an easy project". What I mean by this is that the "difficulty" of a project is something that will uppermost in the mind of the staff marking your thesis. A "difficult" project is likely to be looked upon favourably because it will be a bigger step away from what you have already been taught, you will need to be reading more academic literature, you will be showing more independent learning, and so on. These are some of the most important factors in getting a good grade, and far outweigh factors such as finishing every part of your practical work. The up-shot of this is that if you choose a "difficult" project and complete it quite poorly, you are likely to get better marks than a student who chooses an "easy" project and completes all of their practical work. If you did choose to work on a website-with-a-database-for-an-sme then the proposal will be so easy that you will really have to complete every part of the project perfectly just to get a pass. So, choose a small but difficult project.

 

Have a research question

In the last section I said that a project proposal should pose a problem, not a solution to a problem. Ideally, it is best to phrase this as a research question, such as the following:

• is algorithm X more efficient than algorithm Y?
• is it possible to implement product Z on the cloud?
• can feature L be added to programming language P?
• can theorem T be proven?
• can algorithm Z be adapted to be used in conditions C?

and so on. There are several advantages to this. One is that this is a standard form of writing in academia, and your project will be marked against academic criteria. Secondly, if the aim of your project is to answer a question then you leave the issue of how to answer that question reasonably open ended. It may be that you have a very clear idea, at the start of the project, what you are going to do. That's fine, but as you progress through the project you may well find literature that enlightens your views on how your question can be answered. Thirdly, your answer to the question may not be what you expect. That's fine, it's OK to find out that actually, your algorithm isn't as efficient as you thought, or the theorem cannot be proved, so long as you give solid, convincing evidence for your answer. 

 

Do something practical

If you are working in the sciences, it really is important that you do something practical as part of your work. For these purposes "practical" can mean experimental work or mathematical work -- it's OK to prove a theorem, for example, as the main part of the "practical" content of your work. What you should avoid though, is vague, nebulous, thought-pieces, which have no clear results and cannot be evaluated. Avoid anything with a title like "an investigation into X" or "a dissertation on Y". These sorts of writing are well accepted in the humanities, but for a scientific piece of work you need to propose a question and find some answer to it. Equally, a literature review is not really a project in itself, it needs some research question and evaluation with it to form a complete project.

 

Focus on evaluation from the start

Evaluating your work will likely be the last practical work you complete before finishing your dissertation writing. However, you should know from the start of your project how you plan to do this. As with unit-testing, it is best to have designed you evaluation in as much detail as possible before you start you practical work. That way, you know that what you are aiming for is something that can be evaluated in the manner in which you have planned. Remember, the purpose here is to determine whether your project has answered your original research question.

In general, your evaluation will fall into one of the following categories:

• Performance evaluation: either testing the speed, memory footprint, scalability, load-balancing, or other aspect of the performance of a program or system. This is often the easiest form of evaluation -- it can be performed by a program and so automated, the results can be analysed and presented using a statistics and you will not be reliant on users. Work in programming languages, networking, operating systems, databases, and hardware tend to suit this sort of evaluation well.
• User-acceptance testing and usability: if your project involves creating a product for end-users to test, especially if you have an industrial client, then it is essential that you perform some sort of user acceptance testing. Good options for this are the talk-aloud protocol or semi-structured interviews. NEVER, EVER, EVER think that a "heuristic" evaluation is sufficient. Heuristic methods only catch basic errors, they tell you nothing about how your users will actually experience your product.
• Formal or semi-formal methods: such as proving a theorem, using a model checker (such as SPIN), using a formal method such as B or Z to show that your work is free of particular types of errors.

 

Take (academic) advantage of your supervisor

Every student will have at least one supervisor, who will usually be actively involved in research, consultancy or something similar. This sort of work can provide a wealth of good ideas for projects and has several advantages. Firstly, your supervisor will propose projects that have the right scope and difficulty for your degree course. Secondly, if your supervisor has an interest in what you are doing, they will have a vested interest in seeing you succeed and of course will have a lot of relevant expertise with which they can advise you. Lastly, it is likely that your work will be used by other members of a research group which will give you access to feedback on what you have done.

 

Be flexible (within reason)

Remember that a project is a marathon, not a sprint. It may well be that you get part way along the journey and find out that what you had first set out to do is actually impossible, or impossible within the scope of the project. Or it may be that you find some other way of answering your research question, or you uncover some literature which shows that the question can actually be answered very simply. In this case, you should speak with your supervisor and find a way to reword or even completely change your original research question. This is quite a reasonable thing to do and happens often in "real" research projects, so you should not be worried about it. Your final project does not have to match the original proposal exactly, but you should be able to explain why the changes you made were necessary.

 

Summary

• DO choose a project that will hold your interest for the duration of the project.
• DO NOT choose a project that is the same size or scope as a coursework, or something that is very similar to work you have been set in a module.
• DO propose a "difficult" problem -- it is easier to pass a challenging project than an "easy" one!
• DO propose a research question, and an idea for solving it.
• DO propose a project with some sort of practical or mathematical component, DO NOT set out to write a commentary on a topic.
• DO have a very clear plan for how you will evaluate your project. This should clearly state how you will determine whether or not you have answered your research question.
• DO NOT evaluate an end-user product with only heuristic methods.
• DO test end-user products with real users.
• DO take advantage of the expertise of your project supervisor and their research interests.
• DO be flexible, if you find that your original research question cannot be answered, or if you find that a more "interesting" research question emerges during your project.

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