How do we do research? There are text book answers. Identify your research question. Look for data. Decide on which methods you are going to use. Then start with a literature survey. And so on. My intuition then tells me that what is produced is usually routine, even boring, measured by the small number of citations to any published paper. Can we do better? How can we aim to produce something that is original and significant? I have a jumble of ideas in my mind that I try to organise from time to time for seminars on such topics as ‘research methods’. This is a new attempt to structure the jumble. The motivation: to take the risk of offering advice to researchers – both less and more experienced – and in the process to challenge some of the canons of research ideologies. And also – another kind of risk – to see whether I can draw from my own experience. In this, luck has played a big part – a kind of serendipity. Is there such a thing as planned serendipity? (In my case, none of this was planned.) Maybe wide reading and talking – the breadth as well as the depth?
The first bit of luck was my background in maths and theoretical physics – very employable enabling disciplines (though that wasn’t seen as fashionable at the time). I had a first job at the Rutherford Lab writing the computer programmes to identify bubble chamber events from experiments at CERN. The first piece of luck was that, although working in a team, I was given what in hindsight were enormous responsibilities – at a level I can’t imagine being appropriate for a 22 year old now. This had the advantage of teaching me how to produce things on time – difficult though the work was. Secondly, it was the early days of large main-frame computers and I learned a lot about their enabling significance. I made a decision that became a characteristic of my later career – though heaven knows why I was allowed to do this: I decided to write a general programme that would tackle any event thrown up by the synchrotron. The alternative, much less risky, was to write a suite of much smaller programmes each focused on particular topologies. With hindsight, this was probably unwise though I got away with it. The moral: go for the general if you can. All this was very much ‘blue skies’ research and ‘impact’ was never in my mind.
After a couple of years of this – enjoyable and exciting though it was – I decided that I wanted to do something ‘useful’ – to find a job in the social sciences which would have impact – though we didn’t use that word then. I must have applied for 30 or more jobs and failed to get one. There was very little quantitative social science and the idea of employing someone from theoretical physics was not on anyone’s agenda. So I worked my way into politics and – a long story – ended up on Oxford City Council – which gave me an interest in cities and government which has never left me. And with another piece of luck, I was taken on by a small research group of transport economists in Oxford who had a quantitative problem which demanded ‘big computing’ on the basis that I would do their maths and computing, and they would teach me economics. So I switched fields by a process of apprenticeship.
The research problem – the team funded by the then Ministry of Transport – was the implementation of cost-benefit analysis of large transport projects. This demanded computer models of transport flows in cities – before and after the investment. At the time, the known models were largely in the U.S. and so Christopher Foster, Michael Beesley and I embarked on a tour of the American modellers which included most of those who became iconic names in later years and one of whom became a friend and collaborator over many years. I then started building the model. The standard flow model was a so-called gravity model, based on Newtonian principles but with ‘fudge factors’ added to make it work better. Then a huge chunk of luck for me: I recognised these factors from my student days as being similar to partition functions from statistical mechanics and I was able to rework the basis of the model and shift it from a Newtonian perspective to a Boltzmann statistical averaging one – the so-called entropy maximising models. Around this time, I became Assistant Editor of a new journal – Transportation Research – supporting a Californian, Frank Haight, the Editor. As the copy deadline for Volume 1, Number 3 approached, Frank told me that we didn’t have enough papers, could I help? I offered him my entropy-maximising paper which he gratefully accepted. I had no idea at the time that it would become quite important, but it established my academic and research career. The moral of this: it was not a high impact journal and it was not refereed! And it was driven by a practical problem though it could be seen as basic science – an example of how basic research can emerge from practical concerns.
In the next five years, I made three further moves. The first was to the Ministry of Transport in London where I headed the Mathematical Advisory Unit with the task of building real transport models; then to the Centre for Environmental Studies which gave me the opportunity to broaden my field of research beyond transport; and finally to the University of Leeds. Over a long period – I was in Leeds for a long time – two other general principles emerged and one new idea. First, if you have a good idea in one area – entropy in transport modelling for me – then maximise its use in other areas. Second, if there are alternative approaches to the same problem, explore what is involved in integrating them. The new idea was a basis for building dynamic models of urban growth. I also learned something else about good ideas – especially those that, as in this case, were mathematical: the equations had almost certainly been used in applications in very different domains and these often provided pointers for further development.
Most of this research was carried out in relatively small research groups though in a number of cases – transport models early on, retail models later, there were opportunities for large-scale testing either because of their public investment importance (transport) or commercial value (retail). In small groups – or indeed for individual research – ambition has to be limited; unless, it is possible to switch into what I would call ‘proof-of-concept’ mode where only rough ‘testing’ is possible.
Alan Wilson, March 2015