It is at this point in his career that he ought to be able to present a thesis proposal. This article is concerned with the character and content of such proposals, and it concentrates on this important period of a research student's life. Obviously, the necessity of desirability of this kind of thesis proposal in different Ph.D. programs and/or different sciences is a matter of debate; but that discussion is beyond the scope of this paper. Instead, we concentrate on what we expect of the proposal and on six vital points it should address.
The timing of a thesis proposal is important. For a three-year research program, it should be presented during the second year. If it is done much earlier, it is likely that the problem will not have been well-enough defined or that the candidate will not have done enough background work and/or made enough progress in the area to convince himself and others that he can solve it. If the proposal comes much later, then either there is too little time to do the work before the money runs out or it is a spurious proposal produced after the fact, when the thesis is nearly done.
The form of a thesis proposal is a matter of individual taste of the candidate, his supervisors, and the university. It may be written down in one document, presented orally in seminar, evolved by mutual agreement, or done in some other fashion. It may include research memoranda and/or published articles by the candidate (or coauthored by him). Some parts of it may be eventually included directly in the thesis. The different sections of the proposal may be done in any order, depending upon how the thesis topic was developed. But it is important that it be 'public' at least within the department, so that everyone can know what the candidate is investigating and why.
A thesis proposal in computing science should address at least the following six points:
If the candidate is unable to include these six points in his proposal - or indeed, if he cannot defend them at the corresponding state in his career even if he does not prepare this kind of thesis proposal - then he is not ready to commit himself to the one or two years of blood, sweat, and tears to turn it into an acceptable thesis.
Naturally, neither his supervisor, nor the university, nor his examiners are going to hold him to the details presented in the proposal. The nature of research in this science is that it provides the biggest surprises to those who are most strongly convinced of some fact or idea. When a lot of people are working in a given area at a lot of universities, anyone can be easily 'scooped' or may feel it necessary to revise his plan or problem in mid-stream. He may find that his original ideas do not work and he must modify his expected solution. This is perfectly acceptable, and the plan of research will have to be adapted to fit. Nevertheless, a candidate who is unable to answer the six points is not ready to embark on the work, let alone follow it, control it, and force it to some kind of conclusion.
To prepare the proposal for their benefit is to make a common mistake. Such a proposal is filled with jargon which is private to that local group. It fails to state important constraints and frequently does not provide enough background. Sometimes, the candidate assumes that his supervisors know as much about the specific area of the thesis as he does - something which is often false. Proposals which suffer these faults lack credibility, and it is difficult for the department and the examiners to evaluate the research on its merits. The candidate is then exposed to the real danger that he and supervisors may have been working happily in their own microcosm, only to find that at the end three years he has no results which justify a Ph.D. degree.
To present the problem to the wider audience, and to justify proceeding with the work, it is necessary for the candidate to present the background to the problem and to survey related work by others. This is the second component of a thesis proposal; and is some cases, it may be included directly in the thesis. It may take any of several forms - for example, an annotated bibliography or a comprehensive summary, explanation, and analysis of existing results. It may be necessary or desirable for the candidate to include his own critical comments. For example, it the thesis is to present a new technique for solving a class of numerical problems, then this section of the proposal should review existing techniques and analyse their inadequacies.
This summary/survey/overview is not without its traps. If most of the references cited and most of the work mentioned are from in the candidate's own department (or in one other department with whom he is very 'chummy'), then there are serious grounds for questioning his breadth of knowledge and background for pursuing his problem. The danger is that people who limit their horizons to their own local environments produce very inbred research, narrow attitudes, and unacceptable theses. They tend to reinvent ideas already known elsewhere; they fail to apply techniques which could simplify their problems considerably; they often attach too much importance to minor results and do not recognise major ones worth reporting; and they write incomprehensible theses and papers which make no effective contribution to knowledge. In inbred environments, the work of other organisations is often dismissed as irrelevant or unimportant - characteristic of a disease called NIT (Not Invented Here). It is extremely important for the thesis proposal to indicate that the candidate knows about and accepts such work.
By implication, then, the candidate must have done some successful work in the read, perhaps in collaboration with others, before the thesis proposal. This may be something like the discovery of an interesting algorithm, representation, or relation while working on one of his pre-thesis projects. He recognises this as the tip of the iceberg, the introduction to a new problem area which eventually becomes his thesis research. For example, a student simulating a well-known paging algorithm stumbles across a phenomenon quite different from that which was expected or generally accepted. This result and his subsequent explanation for it form the basis of his thesis proposal and thesis research in memory management. They form the seed of the methods which he develops to specify and solve his problem. Without such results, a plan to investigate the area would have seemed like hot air, and his efforts would have lacked direction. But with them, the success of his research is assured and the timely completion of his thesis is much more likely.
A common situation occurs when a student proposes what seems to be a good problem to investigate, involving new broad, general models or theories. But when he is pressed, he has only some ideas about a small, special case or example. He might not even have explored these ideas fully because he regards that example as uninteresting in the context of the overall problem and those ideas as having no apparent generalisation. Some students will be able to discover the necessary general ideas, develop them and defend them. But such theses are few and far between, and their authors are typically awarded Nobel prizes and other very high distinctions. Ordinary mortals with good first class Honours degrees have no such luck and often get stuck, unable to find any other examples, applications or ideas which are subsequently different from the ones they know already.
At this point, it is time to go back and look at the problem statement again. As often as not, that 'uninteresting' example may be the foundation for an interesting and valuable thesis problem in its own right. If so, it is probably a better investment of the candidate's energy to solve it, finish his thesis, and then devote his life's work to the general problem in a more relaxed fashion.
Occasionally, a research student will say 'I know precisely what problem I want to solve. I have no idea of what the solution will be, but I will certainly recognise it when I've got it. After all, the is research. So how can I possibly give characterisation of the solution beforehand?' That is, he thinks he is an exception, but if he cannot characterise his expected solution, how can he recognise it? More likely, he has not specified his problem sufficiently precisely, or he has not yet done enough preliminary work and obtained some preliminary results in the area of the problem. In either case, he must do more legwork before presenting his thesis proposal.
Sometimes, it is easy to characterise the solution, particularly in the light of preliminary results. For example, a candidate developing a new analytic model to describe message traffic among communicating machines would expect to prove some theorems about the model, validate it empirically against some existing systems, construct some algorithms based on it for calculating the performance of similar systems with different parameters, and argue by example that they are useful in the design and understanding of future systems. At other times, is is much harder to be so specific about a stopping condition. It may also be necessary to change it as the research progresses. However, a moving target is better than no target at all (providing that it is not moving so fast that the candidate cannot catch it).
Finally, it is always useful when doing research to keep in mind how it is to be reported, what issue will be emphasised, and what will be de-emphasised. Thus, the thesis proposal should contain a rough outline of the thesis itself, preferably in terms of the expected solution to the problem. This will have at least a small impact on the shape of the research, and it will provide a set of good guidelines when the candidate decides that it is time to 'write it all up'.
It follows that the thesis proposal as we have described it is not a guarantee of anything and may not always be appropriate. But it helps, particularly when the problem, the investigation, and the expected results are ill-defined. By considering his research in terms of the guidelines we have presented, the candidate, and his supervisors, will go a long way toward developing the sensitivity and awareness necessary to make the research lead to a successful thesis. It is an effort not to be undertaken lightly.
I must acknowledge my deepest debt to Professors Brian Randell, William Lynch, and Bernard Galler, who have taught me enough to be able to recognise a good thesis topic when I see one and to be able to head off at least a few bad ones before the student gets too committed.