Being Interdisciplinary

Front matter

Adventures in urban science and beyond

ALAN WILSON

Adventures in urban science and beyond

Preface

My main objective in this book is to shed light on the question of how to do interdisciplinary research. Insights have emerged, for me, from decades of research and the accumulation of a toolkit, and so this is a personal account. There are two key threads: first, that (almost?) all research is essentially interdisciplinary; and second, that a systems perspective is a good starting point, one that indeed forces us to look beyond disciplines. There is also a more subtle third thread: how to identify the game-changers of the past as a basis for learning to think outside the box of convention — how to do something new, how to be ambitious. In a nutshell, how to be creative.

I will set out some general principles for doing interdisciplinary research which should be widely applicable, whatever the background of the researcher or the nature of the research challenge. I illustrate the practice of interdisciplinary research from my own experience, but I believe that this can be easily related to challenges in the experience of others. In using this material for giving talks and running seminars, I have certainly found this to be the case.

The ideas offered here have been presented to a variety of audiences, ranging from undergraduates, masters and PhD students and early-career researchers — all in a variety of disciplines — through to those with wide experience of interdisciplinary research. In relation to ‘real challenges’ in my own field of urban research, I have had the pleasure of speaking at public meetings with large audiences. On such occasions I have been delighted by the interest shown in the way that research can illuminate the problems in people’s minds.

Iam indebted to Pat Gordon-Smith of UCL Press and two anonymous reviewers for many constructive suggestions which have greatly improved the book; many thanks to Catherine Bradley for her immaculate copyediting and to Grace Patmore for seeing the book through to production. I am also grateful to many students, friends and colleagues who have collaborated and discussed the challenges of interdisciplinary research over the years. Last but far from least, I dedicate this book with thanks to Sarah for her love and support.

Alan Wilson Norfolk, 2021

PREFACE vii

Prologue: a research autobiography

Interdisciplinarity is a complex subject which can be approached in many ways. I have rooted this approach in my personal experience, but aim to draw on general insights which are potentially valuable to readers from a variety of backgrounds — from science via social science to the arts and, not least, the professions. As background, I have set out a brief map of this experience in this prologue.

I have been privileged to encounter a series of partly serendipitous career challenges which took me on an interdisciplinary path before the idea was fashionable. I chart this progression not as a model, but rather as an account of possibilities. This brief account builds on a variety of experiences and choices, as well as the ideas that start to put a rationale round interdisciplinary thinking. I was fortunate in my early career to have the opportunity to spend time in North America, meeting the founding fathers -they were all men — of what became my research field. As a complement to university-based research, I was a founding director of a university spin-out company; here we had to be very business-like, which taught me something about adaptation. I also found myself later venturing into other disciplines, for example being invited ‘in’ to help develop a new research base. Such an experience gives a different perspective on interdisciplinarity.

I was new to geography when I went to Leeds as a Professor in 1970. There was even a newspaper headline in one of the trade papers with words to the effect that ‘Leeds appoints Geography Professor with no qualifications in Geography!’ So how did this come about? As I reflect, it makes me realise the extent to which my career — and this will be by no means unique — has not only been shaped by serendipity, but has also become an illustration of the emergence of interdisciplinarity.

I graduated in mathematics and I wanted to work as a mathematician. I had a summer job as an undergraduate in the (then new) Rutherford Laboratory at Harwell, which led to a full-time post when I left Cambridge. I was, in civil service terms, a ‘Scientific Officer’ - something that I was very pleased about because I wanted to be a ‘scientist’. I even put that as my profession on my new passport. It was an interesting time. I had to write a very large computer program for the analysis of bubble chamber events in experiments at CERN (which also gave me the

PROLOGUE: A RESEARCH AUTOBIOGRAPHY opportunity to spend some time in Geneva). With hindsight, it was very good initial training in what was then front-line computer science.

I also realise, with several decades of hindsight, that this was an early experience of what would now be called ‘data science’. Working in a team, I was given enormous responsibilities — at a level I cannot imagine being thought appropriate for a 22-year-old today. This had the advantage of teaching me how to produce things on time, difficult though the work was. It was also the early days of large, mainframe computers and I learned a lot about their enabling significance.

At Harwell I made a decision that became a characteristic of my later career — though heaven knows why I was allowed to do it. I decided to write a general program that would tackle any event thrown up by the synchrotron. The alternative — much less risky — was to write a suite of far smaller programs, each focused on particular topologies. Again with hindsight this was probably an unwise decision, though I got away with it. The moral is: go for the general if you can. All this was very much ‘blue skies research’ and ‘impact’ was never in my mind.

Within a couple of years, I began to tire of the highly competitive nature of elementary particle physics. I also wanted to work in a field where I could be more socially useful but still be a mathematician. I therefore started applying for jobs in the social sciences in universities: I still wanted to be a maths-based researcher. All the following steps in my career were serendipitous — pieces of sheer good luck.

It did not start well. I must have applied for 30 or 40 jobs and had no positive response at all. To do something different I decided, sometime in 1962, to join the Labour Party. I lived in Summertown in North Oxford, a prosperous part of the city, and there were very few members in the local ward, Summertown. Within months I had taken on the role of Ward Secretary. We selected our candidates for the May 1963 local elections, but around February they left Oxford. It then emerged that, at this short notice, there was no time to select new candidates; the rule book said that the Chairman and Secretary of the Ward would stand instead. So it came about that in May I found myself the Labour candidate for Summertown. I duly came bottom of the poll. I enjoyed it, however, and in the following year I managed to get myself selected for East Ward. This had not had a Labour councillor since 1945, but it seemed just winnable in the prevailing tide.’ I was elected by a majority of four after four recounts. That led me into another kind of experience — three years on Oxford City Council. This was very different from conventional research, but it did add a new dimension to the idea of interdisciplinarity. It was also the beginning of my interest in cities as a prospective subject for research.

Then came a second piece of luck. I was introduced by an old school friend to a small group of economists at the Institute of Economics and Statistics in Oxford who had a research grant from the then Ministry of Transport in cost-benefit analysis. In those days — it seems strange now — social science, even economics, was largely non-quantitative. Yet here they had a very quantitative problem and needed a computer model of transport flows in cities. We struck a deal: that I would do all their maths and computing and they would teach me economics. So I changed fields by a kind of apprenticeship.

It was a terrific time. I toured the United States —- where the highprofile urban modellers were — with Christopher Foster and Michael Beesley,” and we met people such as Britton Harris (the Penn State Study) and I. S ‘Jack’ Lowry (of Model of Metropolis fame). I set about trying to build the model. The huge piece of luck was in recognising that what the American engineers were doing in developing models of flows as ‘gravity models’ could be restated in a format based on Boltzmann and statistical mechanics rather than Newton and gravity. This generalised the methodology. The serendipity in this case was that I recognised some terms in the engineers’ equations from my statistical mechanics lectures as a student, which led to the so-called ‘entropy-maximising models’. I was suddenly invited to give lots of lectures and seminars and people forgot that I had this rather odd academic background.

It was a time of rapid job progression. I moved with Christopher Foster to the Ministry of Transport when he was appointed as Director General for Economic Planning and set up something called the Mathematical Advisory Unit. It grew rapidly with a model-building brief. Thad been given the title of Mathematical Adviser, from which derived the name of the unit. Strictly speaking my title should have been Economic Adviser, but the civil service economists refused to accept me as such because I was not a proper economist. I was summoned to see John Moore, the Assistant Secretary responsible for what we would now call HR. He had obviously been instructed to solve the problem. ‘If you are not an economist, what are you?’ he asked. I replied that I was a mathematician. ‘That’s fine,’ he said, ‘we'll call you the Mathematical Adviser.’

I was in this role from 1966 to 1968, then serendipity struck again. I gave a talk on transport models in the Civil Engineering Department at UCL, and in the audience was Professor Henry Chilver. I had left the seminar and started to walk down Gower Street when he caught up with me. Chilver told me that he had just been appointed as Director of a new research centre, the Centre for Environmental Studies (CES), and ‘would I like to be the Assistant Director?’ My talk had, in effect, been a job

PROLOGUE: A RESEARCH AUTOBIOGRAPHY xi xii interview — not the kind of thing that HR departments would allow now. And so I moved to CES and built a new team of modellers. I worked on extending what I had learned about transport models to the bigger task of building a comprehensive urban model related to the wider planning agenda — something I have worked on ever since.

This was in 1968. By the end of the 1960s, quantitative social science was all the rage. Many jobs were created as universities sought to enter the field and I had three serious approaches: one in geography at Leeds, one in economics and one in town planning. I decided, wisely as it turned out, that geography was a broad church — in a real sense, it is internally interdisciplinary and had a record of absorbing ‘outsiders’. I moved to Leeds in October 1970 as Professor of Urban and Regional Geography. And so I became a geographer. Again, the experience was terrific. I enjoyed teaching. It led to long-term friendships and collaborations with a generation that is still in Leeds, or at least academia: Martin Clarke, Graham Clarke, John Stillwell, Phil Rees, Adrian MacDonald, Christine Leigh, Martyn Senior, Huw Williams and many others — a long list. Some friendships have been maintained over the years with students I met through tutorial groups. We had large research grants and could build modelling teams. Geography, in the wider sense, did prove very welcoming and it was all — or at least mostly — very congenial. Sometime in the early 1970s I found myself as Head of Department and I also started taking an interest in some university issues. That decade was mainly about research, however, and it was very productive.

By the end of the 1970s there had been the oil crisis, cuts were in the air — déjà vu — and research funding was becoming harder to get. My next big step had its origins in a race meeting at a very cold Wetherby on Boxing Day in 1983. I was with Martin Clarke in one of the bars. On the bar’s TV, we were watching Borough Hill Lad, trained near Leeds by Michael Dickinson, win the King George VI Chase at Kempton. Thoughts turned to our lack of research funding. It was at that moment, I think, that we decided to investigate the possibility of commercial applications of our models. Initially we tried to ‘sell’ our ideas to various management consultants, anticipating that they could do the marketing for us. We had no luck, however, so we had to go it alone: a two-person, very part-time workforce.

Our first job was finding the average length of a garden path for the Post Office. Our second was to predict the usage pattern of a projected dry ski slope. We did the programming, collected the data and wrote the reports. Things started looking up when we were awarded substantial contracts by WHSmith and Toyota, as we could then start to employ people. More of this story is told in Chapter 6; it also appears in more detail in Martin Clarke’s recent book.’ What began very modestly became GMAP Ltd, with Martin serving as the Managing Director and driving its growth. At its peak, GMAP was employing 120 people and had a range of blue-chip clients. That was a kind of real geography that I was proud to be associated with. In research terms, it provided access to data that would not normally have been available to academics. The GMAP project was very much ‘research on’ being carried into ‘research for’.

Simultaneously in the 1980s I began to be involved in university management. I became Chairman of the Board of Social and Economic Studies and Law in the university - a Dean, in modern parlance. In 1989 I was invited to become Pro-Vice-Chancellor (PVC) at a time when there was only one such post. I left the geography department — never to return, as it turned out. The then VC became Chairman of the CVCP* and had to spend a lot of time in London, so the PVC job was bigger than usual.

In 1991 I found myself appointed as Vice-Chancellor and embarked on that role — not without some trepidation — on 1 October. I was VC until 2004. The role proved to be challenging, exciting and demanding. It was, in Dickens’ phrase, ‘the best of times and the worst of times’: tremendously privileged, but also with a recurring list of very difficult, sometimes unpleasant problems. I was asked by research friends why I had taken on such a job instead of continuing in research. I responded, at least half seriously, that the job was a serious social science research challenge. But the focus here is research: I somehow managed to keep my academic work going in snatches of time, but my publication rate certainly fell.

I was Vice-Chancellor for almost 13 years, then in 2004 I was scheduled to ‘retire’. This, however, seemed to be increasingly unattractive. Salvation came from an unlikely source: the Department for Education and Skills (DfES) in London. I was offered the job of Director General for Higher Education and so became a civil servant for almost three years, with policy-advising and management responsibilities for universities in England. This brought me direct experience of the ‘P’ in ‘PDA’ — an idea to be explained in Chapter 1 below. Again, it was privileged and seriously interesting to be working with ministers and having a front row seat on the politics of the day.

I always knew I wanted to research again, however, so after a brief sojourn in Cambridge I returned to academic life as Professor of Urban and Regional Systems at UCL. This was another terrific experience. I worked with Mike Batty, an old modelling friend, in the Centre for Advanced Spatial Analysis, along with a group of young researchers.

PROLOGUE: A RESEARCH AUTOBIOGRAPHY xiii xiv

Particularly exciting was the fact that my research field developed into the realms of what became known as ‘complexity science’, a hot topic. Research grants flowed again. This included £2.5M for a five-year grant from EPSRC for a project on global dynamics. This embraced migration, trade, security and development aid: big issues to which real geography can make a significant contribution. The grant funded half a dozen new research posts and five PhD studentships.

The final step was my move to The Alan Turing Institute in the summer of 2016. The original plan was to develop a programme in urban modelling, partly on the basis that modelling was a crucial element of data science which was to some extent being neglected. However, this plan had to be put on hold as, in September, I was appointed as CEO of the Institute. This meant that I had to learn much more than anticipated about data science and AI, which delivered its own research benefits. I began to see new possibilities of urban models being embedded in ‘learning machines’.

My career trajectory has thus taken me from mathematics and elementary particle physics into geography and the social sciences via economics, on to complexity science, and on again into data science and AI. Add to this elements of operational research and ‘management’, both in a university and as a civil servant. The most crucial moves were not planned, so I think that a ‘serendipity label is more than appropriate. As will be obvious, the different roles have always provided the opportunity to learn new skills and to respond to new challenges. I hope the following chapters may help readers who find themselves in similar new situations.

1 Many years later, when I was Vice-Chancellor in Leeds, I was at an event at which Sir John Walker, who had recently been awarded a Nobel Prize, was a guest. I introduced myself to him and he looked me up and down and said, ‘I know you —I canvassed for you in Oxford in 1964’.

2 Foster and Beesley, ‘Estimating the social benefit of constructing an underground railway in London’.

3 Clarke, How Geography Changed the World, and my Small Part in it.

The Committee of Vice-Chancellors and Principals.

5 EPSRCis one of the research councils that are now part of UKRI (UK Research and Innovation) — the Engineering and Physical Sciences Research Council.

r

Chapter 1 Introduction: the organisation of this book

The foundations of this book rest on the conjecture that the most important research problems are essentially interdisciplinary. This does not exclude, of course, important research within disciplines, but such research can usually be seen as an element of something bigger. The argument is constructed in 4 parts and 10 chapters.

Part 1 introduces the systems basis of interdisciplinarity (S), the theory of how a system works (T) and the methods that can be used to represent and work with a system (M) — the STM set of building bricks. This is coupled with a framework for applications of systems research in different kinds of planning with three elements: policy — what are the ‘applied’ objectives (P); design — inventing alternative ways of creating plans and problem solving (D); and analysis — our understanding of the system of interest (A), the PDA framework. The two frameworks complement one another: STM is essentially the analytics basis of PDA. Such a coupling is illustrated by reference to the application of research to ‘real challenges’. This introduction of key concepts in Chapter 1 is followed in Chapter 2 by an exploration of the nature of interdisciplinarity and its relation to traditional disciplines. Two key concepts are introduced here: ‘requisite knowledge’ and ‘combinatorial evolution’.

Part 2 shifts to the practice of interdisciplinary research. It begins with consideration of ‘how to start’ in Chapter 3, followed by the introduction of another core concept — that of a model of a system — in Chapter 4. Research is underpinned by access to data, so Chapter 5 explores the impact of ‘big data’ and ‘data science’ before leading into machine learning and artificial intelligence (AI). The threads of the approach to practice are drawn together through a return to the topic of ‘real challenges’ and problem-solving in Chapter 6.

Part 3 then progresses into expanding the interdisciplinary research toolkit: how to explore the literature — especially understanding the game-changers of the past in Chapter 7. In Chapter 8 we explore the possibilities of translating ideas between domains, including the notion of superconcepts that transcend disciplines.

Part 4 explores the tools needed to manage research (and ourselves as researchers). In Chapter 9 we assess the materials and skills needed —textbooks, courses or experience, opportunities for collaboration, time management and the practice of writing. In Chapter 10 we investigate the organisation of research and its ecosystem of researchers, users and funders.

In this opening chapter, I present in turn the STM and PDA frameworks (pp. 4-6) and then illustrate their application in terms of ‘real challenges’, using my own experience of working on cities as an example (pp. 6-11). I broaden this range of challenges and potential interdisciplinary research problems in the exercises at the end of the chapter.

Key concepts

When I was studying physics I was introduced to the idea of a system of interest: defining at the outset that ‘thing’ you were immediately interested in studying. This is crucial for interdisciplinarity. There are three ideas to be developed from this starting point. First, it is important simply to list all the components of the system; second, to simplify as far as possible by excluding all possible extraneous elements from this list; and third, taking us beyond what the physicists were thinking at the time, to recognise the idea of a ‘system’ as made up of related elements; it was thus as important to understand these relationships as it was to enumerate the components. All three ideas are important. Identifying the components will also lead us into counting them; simplification is the application of Occam’s Razor to the problem; and the relationships take us into the realms of interdependence and complexity. Around the time I was learning about the physicists’ ideas of a ‘system’ something broader, ‘general systems theory’, was in the air, though I did not become aware of it until much later."

So, always start a piece of research with a ‘system of interest’. Defining the system then raises other questions that must be decided at the outset, albeit open to later modification: questions of scale.” There are three dimensions to this. First, what is the granularity at which you view your system components? Population by age: how many age groups? Or age as a continuous variable? Usually too difficult. Second, how do you treat space? Continuous with Cartesian coordinates? Or as discrete zones? If the latter, what size and shape? Third, since we will always be interested in system evolution and change, how do we treat time? Continuously? Or as a series of discrete steps? If the latter, is the focus upon one minute, one hour, one year, 10 years, or what? These choices have to be made in a way that is appropriate to the problem and also, often, in relation to the data which will be needed. (Data collectors have already made these scale decisions.)

Once the system is defined, we have to ask a question along the lines of: how does it work? Our understanding, or ‘explanation’, is represented by a theory. There may be an existing theory, whether partially or fully worked out, or there may be very little theory. Part of the research problem is then to develop the theory, possibly stated as hypotheses to be tested.

Then there is usually a third step relating to further questions. How do we represent our theory? How do we do this in such a way that it can be tested? What methods are available for doing this?°

In summary, a starting point is to define a system of interest, to articulate a theory about how it works and to find methods that enable us to represent, explore and test the theory: the STM approach.

This, through the reference to theory (or hypothesis) formulation and testing, establishes the science base of research. Suppose now that we want to apply our science to real-world problems or challenges. We need to take a further step which is in part an extension of the science; it is still problem-solving in relation to a particular system of interest, but has added dimensions beyond what is usually described as ‘blue skies science’. The additions involve articulating objectives and inventing possible solutions.

Take a simple example: how to reduce car-generated congestion in a city. The science offers us a mathematical-computer model of transport flows. Our objective is to reduce congestion. The possible solutions range from building new roads in particular places to improving a public transport system to divert people from cars. Each possible solution can be thought of as a plan and the whole activity is a form of planning. In some cases, computer algorithms can invent plans, but more usually it is a human activity. For any plan, the new flows can be calculated using the model, along with indicators of, for example, improved traffic speeds and consumers’ surplus. A cost-benefit analysis can be carried out and the plan that has the greatest rate of return or the greatest benefit-to-cost ratio chosen. In reality, of course, it is never as neat as this.*

How can we summarise this process? Many years ago I learned from my friend and collaborator Britton Harris that this can be thought of as policy, design and analysis: a PDA framework to complement the STM approach. His insight was that each of the three elements involved different kinds of thinking — and that it was rare to find these in one person, in one room or applied systematically to real problems. There is a further insight to be gained: the PDA framework can be applied to a problem in ‘pure’ science. The objective, the policy, may be simpler — to articulate a theory — but it is still important to recognise the ‘design’ element: the invention at the heart of the scientific process. Of course, this applies very directly to engineering, as engineers confront both a science problem and a policy and planning problem: both STM and PDA apply.

As we noted briefly, adopting a systems perspective at the outset of a piece of research forces interdisciplinarity. This can be coupled with an idea which will be developed more fully later: requisite knowledge. This is simply the knowledge that is required as the basis for a piece of research. When this question is asked about the system of interest, it will almost always demand elements from more than one discipline; these elements then combine into something new — more than the sum of the parts. There is here a fundamental lesson about effective research: it has to be interdisciplinary at the outset.

This provides a framework for approaching a subject, but we still have to choose. These decisions can be informed but are ultimately subjective. A starting point is that they should be interesting to the researcher but also important so some wider community. The topic should be ambitious but also feasible — a very difficult balance to strike.

Real challenges

Cities provide a system of interest which is complex and interesting, both as science and as science applied to real challenges. Urban research draws on social, economic and geographic disciplines and so provides a good example for our explorations. One starting point is to reflect on the well-known and very real challenges that cities face. The most obvious ones can be classified as ‘wicked problems” in that they have been known for a long time, usually decades, and governments of all colours have made honourable attempts to ‘solve’ them. Given the limited resources of most academic researchers, it could be seen as wishful thinking to take these issues on to a research agenda, but nothing ventured, nothing gained. We need here to bear in mind the PDA framework — policy, design, analysis. Good analysis will demonstrate the nature of the challenges. Policy is usually to make progress with meeting them, while the hard part is the ‘design’ — inventing possible solutions. The analysis comes into play again to evaluate the options. If we focus on the UK context, we can offer a sample of the issues (though most translate easily across national boundaries). Broad headings, reflecting the definition of our system of interest, might be:

1 Living in cities — people issues.

2 The economy of cities — organisations providing goods and services. 3 Urban metabolism: energy and materials flows.

4 Urban form.

5 Infrastructure.

Governance.°

The challenges have all been exacerbated by the COVID pandemic to which we return after pre-pandemic considerations — which are still with us. Consider a sample of issues within each topic.

In this example we see that since the roots lie in social, economic and geographic research, a focus on people at the outset is a good starting point. To illustrate: how do people live in cities? The challenges are well known and can be summarised. Housing: in the UK there is a current shortage and this situation will be exacerbated by population growth. Education — a critical service, upskilling for futureproofing, and yet a significant percentage of young people leave school with inadequate literacy, numeracy and work skills. Health - an uneven delivery of services. The future of work - what will happen if the much predicted ‘hollowing out’ occurs as middle-range jobs are automated? How will those then redundant pay their bills? A complementary perspective focuses on the economy of cities, embracing private and public sectors and the delivery of products, services and jobs (and therefore incomes).