PhD candidate D. Alexander struggles with his fieldwork, circa 1975.
In many instances, the hardest part of writing a PhD thesis is formulating the research questions and any hypotheses that may arise from them.
A research question must be something that does not have an obvious answer. It must not be banal, but equally it must not be obscure. From the outset, there must be a good likelihood of arriving at an answer during three years of concentrated research. It must be something that has not been answered before, or at least not in the manner that the thesis will employ. It must have wider implications than merely finding something out within the strict confines of a field or laboratory data collection exercise.
The first part of doctoral research is a matter of finding out. On the basis of key words (geographical, methodological, philosophical, topical, practical, sectoral, etc., etc.) what problems suggest themselves as amenable to solution and worth tackling? Rarely can research questions be formulated without familiarity with the relevant body of literature, which sets the problems to be solved in the future. So the literature needs to be read critically, with an eye to the issues that it does not succeed in resolving, or the new vistas that it opens. Hence, in doctoral research, the art of reviewing the literature is emphatically not about reporting what has been done. It is a matter of probing the body of research to find out what has not been accomplished, and asking why.
Obviously, many questions are not answered because they are intractable. Most of us could not manage to write a thesis that asks “What is the meaning of life?” Other questions lack substance. Thus, “How many ambulances are there in London?” is not a valid research question, as all it stimulates one to do is to count and find out a simple answer. Doctoral research is about uncovering causal relations and pursuing the implications of the answer to the research question.
In learning how to do research, the biggest hurdle may well be knowing how to ask the question that motivates the study. “How does it work?” may be less important than “Why does it work?” - or “Why does it not work?” or “Why does it not work any better than it actually does?”
Without a good research question (or more likely a set of questions), there is a strong chance that the project will condemn itself to irrelevancy, or even grind to a halt. But why is it so difficult to formulate a viable research question? Why are PhD students so afraid of the other questions: Has it been done before? Can it be done at all? Is it worth doing? What if it all fails?
Here, then, is a strategy for launching the research project.
(a) Start with the key words and use them to define the area of study - theoretically, methodologically, geographically, in terms of scale, discipline, sector, profession, whatever. List as many key words as you like.
(b) Define the body of literature that is pertinent to the field in question. Develop a critique of it, but one that is strictly focussed on the need to define a new research project. It may be necessary to take this step more than once if more than one body of literature is involved.
For example, if the project were about the management of waste generated by the destruction caused by a disaster, there is a discrete literature on the topic and it is not difficult to assemble. We then double-check that we have identified all the most relevant and significant sources and are not missing anything vital. Research in this field has been conducted for 20-23 years. Where has it got us? What is missing from the results? What do the field examples suggest to us (especially the Kobe, TÅhoku and Christchurch earthquakes) about what needs to be done next? What techniques are involved in managing waste, and in developing models? What can be modelled and to what benefit? What are the shortcomings of the analyses? What are the trends in the development of this small field and where do they leave us at present?
(c) List any questions that have not been adequately answered in the research literature. Evaluate them in terms of their potential for study under particular, specified conditions that pertain to the PhD project.
(d) Answers to research questions in disaster risk reduction are not going to be universal. However, they need to have at least some universal relevance. Hence, the questions will be answered in specific contexts, for example, in a particular place or region. The research will need to characterise the answer in terms of the extent to which culture, politics, religion, customs, legal and administrative organisation, and so on, will limit the ability of the findings to be applied elsewhere. Study of a single landslide which devastates a single village may be justified, but only if it offers lessons for similar situations in many other places. If this is not the case, the research will not be worthy of a PhD.
(e) We end up with a question of the sort “What do we need to know next in order to take this field forward?” The exact formulation will respond to what we already know, what we can find out with the available resources, including that of time, and how much the solution contributes to the catalogue of answers to significant problems around the world.
(f) Having defined a workable question, it can be turned into a hypothesis. This is a proposition to be tested, formulated as a tentative statement. Statements like “Country X is not well prepared to manage a tsunami” are not acceptable hypotheses. The statement may be true or false, but there is no depth to the process of verifying it. Already, a statement like “Political polarisation is the main factor that prevents adequate tsunami preparedness” is a little more incisive, as it forces one to look at causal relationships. Hence, a hypothesis must be plausible but probing.
Let me illustrate the process with a word about my own PhD thesis, which I completed in 1977. I should start by pointing out that I did not feel confident to formulate a research project until I was half way through my post-doctoral fellowship. Goodness knows how I got through the PhD, but somehow I did.
I was working in the field of process-based stream-channel geomorphology and either a semi-arid or a Mediterranean environment. Having chosen the latter, I was stuck with the fact that strong seasonal differences complicated the response of landscape to climate. Given that fact, and in addition the impact of tectonics and sea-level change, stream channels in my field area (central southern Italy) lacked integration and equilibrium. They tended to be controlled by base-level fall during episodes of high erosion. Discontinuities migrated up the tributaries. After much reading - about 18 months of it - I decided that the questions I needed to answer were (a) was this a diffusion process and therefore subject to the diffusion equations?, and (b) as turbulence is a diffusion process, does it contribute to homeostasis by diffusing morphological change in loose-boundary channels? A year later, the answers were that discontinuities did seem to migrate by a diffusion process, or at least the model could be made to fit, but turbulent diffusion created oscillations that, although they furthered this process at a strictly local level, rapidly damped out downstream.
The data largely came from a few sections of channel, surveyed in the field, accompanied by a complex process of numerical simulation. Did the answers have any relevance outside the area surveyed, indeed, even in the next drainage basin 15 km away? Yes, as the analysis touched on some rather fundamental issues. One of those was ”Does randomness exist?” Not that I could provide a definitive answer, but it was interesting to speculate (yes it does, but largely as a convenient generalisation of complex deterministic processes). Another question was, “Is there a distinctive landscape shaped by the Mediterranean climate’s annual oscillations?” The answer, once again highly provisional, was no there isn’t, except in terms of the speed and rhythm with which morphological change occurs. In the end, the analysis carried out for the thesis tackled some theoretical issues (how discontinuities propagate through stream longitudinal profiles) and had a dig at some deeper philosophical questions. That was enough. No doubt it has all been roundly surpassed by subsequent research, but it was a good training in the scientific method.
In conclusion, the first research question should be “What is wrong with the research?” Dissatisfaction with existing answers is a very good motivation for finding new ones.
A research question must be something that does not have an obvious answer. It must not be banal, but equally it must not be obscure. From the outset, there must be a good likelihood of arriving at an answer during three years of concentrated research. It must be something that has not been answered before, or at least not in the manner that the thesis will employ. It must have wider implications than merely finding something out within the strict confines of a field or laboratory data collection exercise.
The first part of doctoral research is a matter of finding out. On the basis of key words (geographical, methodological, philosophical, topical, practical, sectoral, etc., etc.) what problems suggest themselves as amenable to solution and worth tackling? Rarely can research questions be formulated without familiarity with the relevant body of literature, which sets the problems to be solved in the future. So the literature needs to be read critically, with an eye to the issues that it does not succeed in resolving, or the new vistas that it opens. Hence, in doctoral research, the art of reviewing the literature is emphatically not about reporting what has been done. It is a matter of probing the body of research to find out what has not been accomplished, and asking why.
Obviously, many questions are not answered because they are intractable. Most of us could not manage to write a thesis that asks “What is the meaning of life?” Other questions lack substance. Thus, “How many ambulances are there in London?” is not a valid research question, as all it stimulates one to do is to count and find out a simple answer. Doctoral research is about uncovering causal relations and pursuing the implications of the answer to the research question.
In learning how to do research, the biggest hurdle may well be knowing how to ask the question that motivates the study. “How does it work?” may be less important than “Why does it work?” - or “Why does it not work?” or “Why does it not work any better than it actually does?”
Without a good research question (or more likely a set of questions), there is a strong chance that the project will condemn itself to irrelevancy, or even grind to a halt. But why is it so difficult to formulate a viable research question? Why are PhD students so afraid of the other questions: Has it been done before? Can it be done at all? Is it worth doing? What if it all fails?
Here, then, is a strategy for launching the research project.
(a) Start with the key words and use them to define the area of study - theoretically, methodologically, geographically, in terms of scale, discipline, sector, profession, whatever. List as many key words as you like.
(b) Define the body of literature that is pertinent to the field in question. Develop a critique of it, but one that is strictly focussed on the need to define a new research project. It may be necessary to take this step more than once if more than one body of literature is involved.
For example, if the project were about the management of waste generated by the destruction caused by a disaster, there is a discrete literature on the topic and it is not difficult to assemble. We then double-check that we have identified all the most relevant and significant sources and are not missing anything vital. Research in this field has been conducted for 20-23 years. Where has it got us? What is missing from the results? What do the field examples suggest to us (especially the Kobe, TÅhoku and Christchurch earthquakes) about what needs to be done next? What techniques are involved in managing waste, and in developing models? What can be modelled and to what benefit? What are the shortcomings of the analyses? What are the trends in the development of this small field and where do they leave us at present?
(c) List any questions that have not been adequately answered in the research literature. Evaluate them in terms of their potential for study under particular, specified conditions that pertain to the PhD project.
(d) Answers to research questions in disaster risk reduction are not going to be universal. However, they need to have at least some universal relevance. Hence, the questions will be answered in specific contexts, for example, in a particular place or region. The research will need to characterise the answer in terms of the extent to which culture, politics, religion, customs, legal and administrative organisation, and so on, will limit the ability of the findings to be applied elsewhere. Study of a single landslide which devastates a single village may be justified, but only if it offers lessons for similar situations in many other places. If this is not the case, the research will not be worthy of a PhD.
(e) We end up with a question of the sort “What do we need to know next in order to take this field forward?” The exact formulation will respond to what we already know, what we can find out with the available resources, including that of time, and how much the solution contributes to the catalogue of answers to significant problems around the world.
(f) Having defined a workable question, it can be turned into a hypothesis. This is a proposition to be tested, formulated as a tentative statement. Statements like “Country X is not well prepared to manage a tsunami” are not acceptable hypotheses. The statement may be true or false, but there is no depth to the process of verifying it. Already, a statement like “Political polarisation is the main factor that prevents adequate tsunami preparedness” is a little more incisive, as it forces one to look at causal relationships. Hence, a hypothesis must be plausible but probing.
Let me illustrate the process with a word about my own PhD thesis, which I completed in 1977. I should start by pointing out that I did not feel confident to formulate a research project until I was half way through my post-doctoral fellowship. Goodness knows how I got through the PhD, but somehow I did.
I was working in the field of process-based stream-channel geomorphology and either a semi-arid or a Mediterranean environment. Having chosen the latter, I was stuck with the fact that strong seasonal differences complicated the response of landscape to climate. Given that fact, and in addition the impact of tectonics and sea-level change, stream channels in my field area (central southern Italy) lacked integration and equilibrium. They tended to be controlled by base-level fall during episodes of high erosion. Discontinuities migrated up the tributaries. After much reading - about 18 months of it - I decided that the questions I needed to answer were (a) was this a diffusion process and therefore subject to the diffusion equations?, and (b) as turbulence is a diffusion process, does it contribute to homeostasis by diffusing morphological change in loose-boundary channels? A year later, the answers were that discontinuities did seem to migrate by a diffusion process, or at least the model could be made to fit, but turbulent diffusion created oscillations that, although they furthered this process at a strictly local level, rapidly damped out downstream.
The data largely came from a few sections of channel, surveyed in the field, accompanied by a complex process of numerical simulation. Did the answers have any relevance outside the area surveyed, indeed, even in the next drainage basin 15 km away? Yes, as the analysis touched on some rather fundamental issues. One of those was ”Does randomness exist?” Not that I could provide a definitive answer, but it was interesting to speculate (yes it does, but largely as a convenient generalisation of complex deterministic processes). Another question was, “Is there a distinctive landscape shaped by the Mediterranean climate’s annual oscillations?” The answer, once again highly provisional, was no there isn’t, except in terms of the speed and rhythm with which morphological change occurs. In the end, the analysis carried out for the thesis tackled some theoretical issues (how discontinuities propagate through stream longitudinal profiles) and had a dig at some deeper philosophical questions. That was enough. No doubt it has all been roundly surpassed by subsequent research, but it was a good training in the scientific method.
In conclusion, the first research question should be “What is wrong with the research?” Dissatisfaction with existing answers is a very good motivation for finding new ones.
