51. Research strategy for funders

UK Research and Innovation (UKRI) is a key node in a complex UK – indeed international – research ecosystem.  It can offer strategic direction and for many it will a key funder.  How are the strategic priorities of an ecosystem categorised?  I am a researcher who has worked in a national Institute (today it is the Rutherford Lab) and as a university professor building research teams on Research Council grants.  I was a founder and director of a spin-out company, a university vice-chancellor, Chair of a Research Council and, currently, CEO of The Alan Turing Institute. In all these activities, there are common questions and challenges.  There is a need to acquire a knowledge of the current landscape, decisions on where to invest resources and on how to build capacity and skills.  There is also the question of how to connect a top-down strategy with bottom-up creativity.  All of these are challenges for UKRI.

Where are the potential game changers in research?  Some will be rooted in pure science, while others will be related to wider societal challenges, like curing cancer.  Another key consideration is where knowledge can be applied. That can be used as a working definition of ‘innovation’.

A systems view

So, how to set about answering these questions?  A systems perspective is nearly always valuable: what is the system of interest and how is it embedded in other systems?  Note that a systems perspective requires an interdisciplinary perspective. At what scale is the research to be focussed?  Any system of interest will in fact be embedded in a hierarchy of supra-systems and sub-systems. Recall the Brian Arthur argument:  most innovation comes from the lower reaches of the hierarchy; and what is more, these discoveries can often be transferred to other domains.  Take computers, for example: invented as calculating machines, now ubiquitous in a wide range of systems. Contributions to strategy can come top-down from institutions (reading the landscape and horizons scanning) or bottom-up from individual researchers.

Impact also plays an important part.  Does anyone want to do research that has no impact? I doubt it, but ‘impact’ should include transformative change in and across disciplines just as much as in industry and the public sector. Perhaps, we have been too narrow in our definition of impact.

Establishing a base

These challenges, questions and approaches have to be addressed at each node in the ecosystem.  Then the nodes must be effectively connected.  For example, money has to flow in the direction of the potential game-changers and the high impact innovations.  Each node, from the individual piece of research up to UKRI has to have a strategy, grounded in experience, but employing horizon scanning and imagination.

The ecosystem has not been functioning effectively for some time – notably in the transfer of research findings into industry and the public sector.  Herein lies a particular challenge for UKRI.  Its strategy has to: be open to the ‘bottom up’; incentivise Research Councils, Innovate UK, the universities, the Research Institutes and, not least, industry.  It needs to do all these things if it is to have a chance of delivering game-changers and ground-breaking innovations.

Building a strategy

To build an effective strategy, UKRI will have to:

  • identify and build on strengths and opportunities – both the people with track records and the early career researchers with skills, imagination and ambition – there is a top-down vs bottom-up aspect here;
  • find ways of avoiding the conservatism of peer review which is enforced by the Research Excellence Framework.  I believe that universities do not always provide the right incentives by insisting on both the volume of publication and focusing for promotion on ‘top journals’. This has skewed the motivation of researchers, particularly by neglecting applied research whose outputs do not qualify for the selected journals.

Industry has a role to play.  Where are the modern equivalents of Bell Labs? How much R&D is now being done in start-ups with the big players relying on purchasing success?  While there are many excellent examples of industry-university joint working, there could perhaps be many more.

Another strategic question which demands sensitive judgement relates to the size of research groups.  What should be located at the ‘big science’ end of the spectrum?  There are established successes, from CERN to Sanger; there are new Institutes like Turing and Diamond, with others in development.  Yet is the average size of a research group in a university too small?  Are there potential ‘big science’ areas that are not funded as such? Cities, for example, falls into this category.

Indeed, how do we value different fields of research for public funding? Health, education, justice – all are obviously important.  Basic research is needed to support future industrial development.  Should there be more applied research as well, both in industry or the public sector?

Radical shifts

In the 1950s, Warren Weaver was the Science Vice-President of the Rockefeller Foundation.  He argued that systems of interest fell into three categories, those:

  • that were simple;
  • of disorganised complexity;
  • of organised complexity.

Roughly speaking, the first two represented (among other things) the physical sciences of the time, while the third comprised biology.  He switched his funding from physics to biology.  That was a prescient decision. Is there an equivalent diagnosis to be made now?

UKRI’s strategy needs to be connected to the social questions of our time: climate change and sustainability; the future of work and incomes; growing social inequalities.  Does this agenda demand a Weaver-like shift?

While I have focussed on questions specifically relating to UKRI strategy, in reality, every element of the research ecosystem needs strategic thinking: from universities and institutes, through industry and Government Departments, to individual researchers.  All of it needs to be strongly connected to translational and development ecosystems.

50. Management: do you really need an MBA?

‘How to manage’ has itself become big business – note the success of University Business Schools and the MBA badge that they offer; note the size of the management section of a bookshop. I don’t dispute the value of management education or of much of the literature, but my own experience has been different: learning on the job. It is interesting, for myself at least, to trace the evolution of my own knowledge of ‘management’. I don’t claim this as a recipe for success. There were failures along the way, and I have no doubt that there are many alternative routes. But I did discover some principles that have served me well – most of them filleted from the literature, tempered with experience.

In my first ten years of work, my jobs were well focused, with more or less single objectives and ‘management’ consisted of getting the job done. This began, at the newly founded Rutherford Laboratory at Harwell, writing computer programmes to identify bubble chamber events at the CERN synchrotron; on to implementing transport models for planning purposes at the then Ministry of Transport. I set up the Mathematical Advisory Unit in the Ministry, which became large and doing this was clearly a management job. I moved to the Centre for Environmental Studies as Assistant Director – another management job. These roles were on the back of a spell of research into urban economics and modelling in Oxford which also had me working on a broader horizon even when I was a civil servant – and of course, CES was a research institute. From 1964-67 I was an Oxford City Councillor (Labour) – then a wholly ‘part-time’ occupation on top of my other jobs.

What did I learn in those ten years? At the Rutherford Lab, the value of teamwork and being lightly managed by the two layers above me and being given huge responsibilities in the team at a very young age. In MoT, I learned something about working in the Civil Service though my job was well-defined; again, I had sympathetic managers above me. On Oxford Council, I learned the working of local government, and how a political party worked, at first hand. This was teamwork of a different kind. At CES, I built my own team. At both MoT and CES I recruited some very good people who went on to have distinguished careers. In all cases, the working atmosphere was pretty good. It was in CES, however, that I realise with hindsight that I made a big mistake. I assumed that urban modelling was the key to the future development of planning, probably convinced Henry Chilver, the Director of this, and I neglected the wider context and people like Peter Wilmott from whom I should have learned much more. That led to the Director being fired as the Trustees sought to widen the brief – or to bring it back to its original purpose, and it nearly cost me my job (as I learned from one of the Trustees) but fortunately, it didn’t. It was also my first experience of a govering body – the Board of Trustees – and another mistake was to leave the relationship with them entirely with the Director – so I had no direct sense of what they were thinking. I left a few months later for the University of Leeds and within a couple of years, I began to have the experience of broader-based management jobs.

I went to Leeds as Professor of Urban and Regional Geography into a School of Geography that was being rebuilt through what would be described as strong leadership but which amounted to bullying at times. I was left to get on with my job, I enjoyed teaching and I was successful in bringing in research grants and I built a good team. The atmosphere, however, was such that after two nor three years, I was thinking of leaving. Out of the blue, the Head of Department was appointed as a Polytechnic Head and I found myself as Head of Department. The first management task was to change the atmosphere and an important element of that was to make the monthly staff meeting really count – a key lesson – ‘leadership’ should be through the consent of the staff and this was something I could more or less maintain in later jobs. This isn’t as simple as it sounds of course, there are often difficult disagreements to be resolved. The allocation of work round the staff of the Department was very uneven and I managed to sort that out with a ‘points’ system. I learned the value of PR as the first Research Assessment Exercise approached – by making sure we publicised our research achievements and this helped us to a top rating (which wasn’r common in the University at the time).

The Geography staff meeting was my first experience of chairing something and I probably learned from my predecessor – how not to do it, how to ensure that you secure the confidence, as far as possible, of the people in the room. I was elected as Head of Department for three three-year spells, alternating with my fellow Professor. I began to take on University roles, and in particular to chair one of the main committees – the Research Degrees Committee – and this led to me being Chair of the Joint Board of the Faculties of Arts, Social and Economic Studies and Law – equivalent of a Dean in modern parlance – which represented a large chunk of the University and was responsible for a wide range of policy and administration. There were many subcommittees. So lots of practice. The Board itself had something of the order of 100 members.

In the late 80s, I was ‘elected’ – quotation marks as there was only one candidate! – as Pro-Vice-Chancellor for 1989-91. There was only one such post at the time and the then VC became Chair of CVCP for those two years and delegated a large chunk of his job to me. The University was not in awful shape, but not good either. Every year, there was a big argument about cuts to departmental budgets. I began thinking about how to turn the ‘ship’ around – a new management challenge on a big scale. It helped that at the end of my first year as PVC, I was appointed as VC-elect from October 91, so in my second year, I could not only plan, but begin to implement some key strategies. It’s a long story so I will simply summarise some key elements – challenges and the beginnings of solutions.

The University had 96 departments and was run through a system of over 100 committees (as listed in the University Calendar) – seriously schlerotic. For example, there were seven Biology Departments each mostly doing molecular biology. We had to shift the ‘climate’ from one of cost cutting to one of income generation and this was done through delegation of budgets to each of a reduced number of departments (96 to 55) which was based on cost management but critically, with delegated income generating rules – and this became the engine for both growth and transformation. There were winners and losers of course and this led to some serious handling challenges at the margins. (I tried to resolve these by going to department staff meetings to take concerns head on. That sometimes worked, sometimes didn’t!) There was a challenge of how to marry department plans with the University’s plan. The number of committees was substantially reduced – indeed with a focus on three key committees.

In my first two years as VC, there was a lot of opposition to the point where I even started thinking about the minimum number of years I would have to do to leave in a respectable way. By the third year, many of those who had been objecting had taken early retirement and the management responsibilities around the University – Heads of Department, members of key committees – were being filled by a new generation. I ended up staying in post for thirteen years.

Can I summarise at least some of the key principles I learned in that time?

  • Recognising that the University was not a business, but had to be business-like.
  • Having our own strategy within a volatile financial and policy environment; then operating tactically to bring in the resources that we needed to implement our strategy.
  • What underpins my thinking about strategy is an idea that I learned from my friend Britton Harris of the University of Pennsylvania in the 1970s. He was a city planner (and urban model builder) and he argued that planning involved three kinds of thinking: policy, design and analysis with the added observation that ‘you very rarely find all three in the same room at the same time’. Apply this to universities: ‘analysis’ means understanding the business model and having all relevant information to hand; ‘policy’ means specifying objectives; ‘design’ means inventing possible plans and working towards identifying the best – which becomes the core strategy. This may well be the most valuable part of my toolkit.
  • Recognising that a large institution – by the end of my period, 33,000 students and 7,000 staff – could not be ‘run’ from the centre, so an effective system of real delegation was critical.
  • The importance of informal meetings and discussions – outside the formal committee system; I had at least termly meetings with all Heads of Department, with members of Council, with the main staff unions, with the Students Union Executive.
  • Openness: particularly of the accounts.
  • Accountability: in reorganising the committee system, I retained a very large Senate – about 200 of whom around half would regularly come to meetings.
  • And something not in the job description: realising that how I behaved somehow had an impact on the ethos of the University.

By many measures, I was successful as a manager and I learned most of the craft as a Vice-Chancellor. But I was constantly conscious of what I wasn’t succeeding at so I’m sure my ‘blueprint’ is a partial one. I learned a lot from the management literature. Mintzberg showed me that if in an organisation, your front-line workers are high-class professionals, if they didn’t feel involved in the management, you would have problems. (In this respect, I think the university system in the UK has done pretty well, the health service, less so.) Ashby taught me the necessity to devolve responsibility, Christensen taught me about the challenges of disruption and how to work around them. I learned a lot about developing strategy and the challenges of implementation – “strategy is 5% of the problem, implementation is 95%”. I learned a lot about marketing. I tried to encapsulate much of this in running seminars for my academic colleagues and for the University administration. Much later, I wrote a lot of it up in my book, Knowledge power.

So do you really need an MBA? I admire the best of them and their encapsulated knowledge. In my case, I guess I had the apprenticeship version. Over time, it is possible to build an intellectual management toolkit in which you have confidence that it more or less works. I have tried to stick to these principles in subsequent jobs – UCL, AHRC, The Alan Turing Institute. Circumstances are always different, and the toolkit evolves!

Alan Wilson

49. OR in the Age of AI

In 2017, I was awarded Honorary Membership of the Operational Research Society. I felt duly honoured, not least because I had considered myself, in part, an operational researcher since the 1970s and had indeed published in the Society’s Journal and was a Fellow at a time when that had a different status. However, there was a price! For the following year, I was invited to give the annual Blackett Lecture, delivered to a large audience at the Royal Society in November last year. The choice of topic was mine. Developments in data science and AI are impacting most disciplines, not least OR. I thought that was something to explore and that gave me a snappy title: OR in the Age of AI.

OR shares the same enabling disciplines as data science and AI and (in outline) is concerned with system modelling, optimisation, decision support, and planning and delivery. The systems focus forces interdisciplinarity and indeed this list shows that insofar as it is a discipline, it shares its field with many others. If we take decision support and planning and delivery as at least in part distinguishing OR, then we can see it is applied and it supports a wide range of customers and clients. These have been through three industrial revolutions and AI promises a fourth. We can think of these customers, public or private, as being organisations driven by business processes. What AI can do is read and write, hear and see, and translate, and these wonders will transform many of these business processes. There will be more complicated shifts – driving robotics, including soft robotics, understanding markets better, using rules-based algorithms to automate processes – some of them large-scale and complicated. In many ways all this is classic OR with new technologies. It is ground-breaking, it is cost saving, and does deplete jobs. But in some ways it’s not dramatic.

The bigger opportunities come from the scale of available data, computing power and then two things: the ability of systems to learn; and the application to big systems, mainly in the public sector, not driven in the way that profit-maximising industries are. For OR, this means that the traditional roles of its practitioners will continue, albeit employing new technologies; and there is a danger that because these territories overlap across many fields – whether in universities or the big consultancies – there will be many competitors that could shrink the role of OR. The question then is:  can OR take on leadership roles in the areas of the bigger challenges?

Almost every department of Government has these challenges – and indeed many of them – say those associated with the criminal justice system – embrace a range of government departments, each operating in their own silos, not combining to collect the advantages that could be achieved if they linked their data. They all have system modelling and/or ‘learning machine’ challenges. Can OR break into these?

The way to break in is through ambitious proof-of-concept research projects – the ‘R’ part of R and D – which then become the basis for large scale development projects, the ‘D’. There is almost certainly a systemic problem here. There have been large scale ambitious projects – usually concerned with building data systems – arguably a prerequisite – and many of these fail. But most of the funded research projects are relatively small and the big ‘linking’ projects are not tackled. So the challenge for OR, for me, is to open up to the large-scale challenges, particularly in government, to ‘think big’.

The OR community can’t do this alone, of course. However, there is a very substantial OR service in government – one of the recognised analytics professions – and there is the possibility of asserting more influence from within. But the Government itself has a responsibility to ensure that its investment in research is geared to meet these challenges. This has to be a UKRI responsibility – ensuring that research council money is not too thinly spread, and ensuringthat research councils work effectively together as most of the big challenges are interdisciplinary and cross-council. Government Departments themselves should both articulate their own research challenges and be prepared to fund them.

Alan Wilson

48. Mix and match: The five pillars of data science and AI

There are five pillars of data science and AI. Three make up, in combination, the foundational disciplines – mathematics, statistics and computer science; the fourth is the data – ‘big data’ as it now is; and the fifth is a many-stranded pillar – domain knowledge. The mathematicians use data to calibrate and test models and theories; the statisticians also calibrate models and seek to infer findings from data; the computer scientists develop the intelligent infrastructure (cf Blog 47). Above all, the three combine in the development of machine learning – the heart of contemporary AI and its applications. Is this already a new discipline? Not yet, I suspect – not marked by undergraduate degrees in AI (unlike, say, biochemistry). These three disciplines can be thought of as enabling disciplines and this helps us to unpick the strands of the fifth pillar: both scientists and engineers are users, as are the applied domains such as  medicine, economics and finance, law, transport and so on. As the field develops, the AI and data science knowledge will be internalised in many of these areas – in part meeting the Mike Lynch challenge (see Blog 46) incorporating prior knowledge into machine learning.

Even this brief introduction demonstrates that we are in a relatively new interdisciplinary field. It is interesting to continue the exploration by connecting to previous drivers of interdisciplinarity – to see how these persist and ‘add’ to our agenda; and then to examine examples of new interdisciplinary challenges.

It has been argued in earlier posts that the concept of a system of interest drives interdisciplinarity and this is very much the case here in the domains for which the AI toolkit is now valuable. More recently, complexity science was an important driver with challenges articulated through Weaver’s notion of ‘systems of organised complexity’. This emphasises both the high dimensionality of systems of interest and the nonlinear dynamics which drives their evolution. There are challenges here for the applications of AI in various domains. Handling ‘big data’ also drives us towards high dimensionality. I once estimated the number of variables I would like to have to describe a city of a million people at a relatively coarse grain, and the answer came out as 1013! This raises new challenges for the topologists within mathematics: how to identify structures within the corresponding data sets – a very sophisticated form of clustering! These kinds of system can be described through conditional probability distributions again with large numbers of variables – high dimensional challenges for Bayesian statisticians. One way to proceed with mathematical models that are high dimensional and hence intractable is to run them as simulations. The outputs of these models can then be treated as ‘data’ and, to my knowledge, there is an as-yet untouched research challenge: to apply unsupervised machine learning algorithms to these outputs to identify structures in a high-dimensional nonlinear space.

We begin to reveal many research challenges across both foundational, and especially, applied domains. (In fact a conjecture is that the most interesting foundational challenges emerge from these domains?) We can then make another connection – to Brian’s Arthur’s argument in his book The nature of Technology. A discovery in one domain can, sometimes following a long period, be transferred into other domains: opportunities we should look out for.

Can we optimise how we do research in data science and AI? We have starting points in the ideas of systems analysis and complexity science: define a system of interest and recognise the challenges of complexity. Seek the data to contribute to scientific and applied challenges – not the other way round – and that will lead to new opportunities? But perhaps above all, seek to build teams which combine the skills of mathematics, statistics and computer science, integrated through both systems and methods foci. This is non-trivial, not least due to the shortage of these skills. In the projects in the Turing Institute funded by the UKRI Special Priorities Fund – AI for Science and Government (ASG) and Living with machines (LWM) – we are trying to do just this. Early days and yet to be tested. Watch this space!

Alan Wilson

47. What is ‘data science? What is ‘AI’?

When I first took on the role of CEO at The Alan Turing Institute, the strap line beneath the title was ‘The National Institute for Data Science’. A year or so later, this became ‘The National Institute for Data Science and AI’ – at a time when there was a mini debate about whether there should be a separate ‘national institute for AI’. It has always seemed to me that ‘AI’ was included in ‘data science’ – or maybe vice versa. In the early ‘data science’ days, there were plenty of researchers in Turing focused on machine learning for example. However, we acquired the new title – ‘for avoidance of doubt’ one might say – and it now seems worthwhile to unpick the meanings of these terms. However we define them, there will be overlaps but by making the attempt, we can gain some new insights.

Ai has a long history, with well-known ‘summers’ and ‘winters’. Data science is newer and is created from the increases in data that have become available (partly generated  by the Internet of Things) closely linked with continuing increases in computing power. For example, in my own field of urban modelling, where we need location data and flow data for model calibration, the advent of mobile phones means that there is now a data source that locates most of us at any time – even when phones are switched off. In principle, this means that we could have data that would facilitate real-time model calibration. New data, ‘big data’, is certainly transforming virtually all disciplines, industry and public services.

Not surprisingly, most universities now have data science (or data analytics) centres or institutes – real or virtual. It has certainly been the fashion but may now be overtaken by ‘AI’ in that respect. In Turing, our ‘Data science for science’ theme has now transmogrified into ‘AI for science’ as more all embracing. So there may now be some more renaming!

Let’s start the unpicking. ‘Big data’ has certainly invigorated statistics. And indeed, the importance of machine learning within data science is a crucial dimension – particularly as a clustering algorithm with obvious implications for targeted marketing (and electioneering!). Machine learning is sometimes called ‘statistics reinvented’! The best guide to AI and its relationship to data science that I have found is Michael Jordan’s blog piece ‘Artificial intelligence – the revolution hasn’t happened yet’ – googling the title takes you straight there. He notes that historically AI stems from what he calls ‘ human-imitative’ AI; whereas now, it mostly refers to the applications of machine learning – ‘engineering’ rather than mimicking human thinking. As this has had huge successes in the business world and beyond, ‘it has come to be called data science’ – closer to my own interpretation of data science, but which, as noted, fashion now relabels as AI.

We are a long way from machines that think and reason like humans. But what we have is very powerful. Much of this augments human intelligence, and thus, following Jordan, we can reverse the acronym: ‘IA’ is ‘intelligence augmentation’ – which is exactly where the Turing Institute works on rapid and precise machine-learning-led medical diagnosis – the researchers working hand in hand with clinicians. Jordan also adds another acronym: ‘II’ – ‘intelligent infrastructure’. ‘Such infrastructure is  beginning to make its appearance in domains such as transportation, medicine, commerce and finance, with vast implications for individual humans and societies.’ This is a bigger scale concept than my notion that an under-developed field of research is the design of (real-time) information systems.

This framework, for me, provides a good articulation of what AI means now – IA and II. However, fashion and common useage will demand that we stick to AI! And it will be a matter of personal choice whether we continue to distinguish data science within this!!

Alan Wilson

46. Moving on 2: pure vs applied

In my early days as CEO in Turing, I was confronted with an old challenge: pure vs applied though often in a new language – foundational vs consultancy for example. In my own experiences from my schooldays onwards, I was always aware of the higher esteem associated with the ‘pure’ and indeed leaned towards that end of the spectrum. Even when I started working in physics, I worked in ‘theoretical physics’. It was when I converted to the social sciences that I realised that my new fields, I could have it both ways: I worked on the basic science of cities through mathematical and computer modelling but with outputs that were almost immediately applicable in town and regional planning. So where did that kind of thinking leave me in trying to think through a strategy for the Institute?

Oversimplifying: there were two camps – the ‘foundational’ and the ‘domain-based’. Some of the former could characterise the latter as ‘mere consultancy’. There were strong feelings. However, there was a core that straddled the camps: brilliant theorists, applying their knowledge in a variety of domains. It was still possible to have it both ways. How to turn this into a strategy – especially given that the root of a strategic plan will be the allocation of resources to different kinds of research? In relatively early days, it must have been June 2017, we had the first meeting of our Science Advisory Board and for the second day, we organised a conference, inviting the members of our Board to give papers. Mike Lynch gave a brilliant lecture on the history of AI through its winters and summers with the implicit question: will the present summer be a lasting one? At the end of his talk, he said something which has stuck in my mind ever since: “The biggest challenge for machine learning is the incorporation of prior knowledge”. I would take this further and expand ‘knowledge’ to ‘domain knowledge’. My intuition was that the most important AI and data science research challenges lay within domains – indeed that the applied problems generated the most challenging foundational problems.

Producing the Institute’s Strategic Plan in the context of a sometimes heated debate was a long drawn out business – taking over a year as I recall. In the end, we had a research strategy based on eight challenges, six of which were located in domains: health, defence and security, finance and the economy, data-centric engineering, public policy and what became ‘AI for science’. We had two cross-cutting themes: algorithms and computer science, and ethics. The choice of challenge areas was strongly influenced by our early funders:  the Lloyds Register Foundation, GCHQ and MoD, Intel and HSBC. Even without a sponsor at that stage, we couldn’t leave out ‘health’! All of these were underpinned by the data science and machine learning methods tool kit. Essentially, this was a matrix structure: columns as domains, rows as method – an effective way of relaxing the tensions, of having it both ways. This structure has more or less survived, though with new challenges added – ‘cities’ for example and the ‘environment’.

When it comes to allocating resources, other forces come into play. Do we need some quick wins? The balance between the short term and the longer – the latter inevitably more speculative? Should industry fund most of the applied? This all has to be worked in the context of a rapidly developing Government research strategy (with the advent of UKRI) and the development of partnerships with both industry and the public sector. There is a golden rule, however, for a research institute (and for many other organisations such as universities): think through your own strategy rather than simply ‘following the money’ which is almost always focused on the short term. Then given the strategy, operate tactically to find the resources to support it.

In making funding decisions, there is an underlying and impossible question to answer: how much has to be invested in an area to produce results that are truly transformative? This is very much a national question but there is a version of it at the local level. Here is a conjecture: that transformative outcomes in translational areas demand a much larger number of researchers to be funded than to produce such transformations in foundational areas. This is very much for the ‘research’ end of the R and D spectrum – I can see that the ‘D’ – development – can be even more expensive. So what did we end up with? The matrix works and at the same time acknowledges the variety of viewpoints. And we are continually making judgements about priorities and the corresponding financial allocations. Pragmatism kicks in here!

Alan Wilson

45. Moving on 1: collaboration

I left CASA in UCL in July 2016 and moved to the new Alan Turing Institute. I’d planned the move to give me a new research environment – as a Fellow with some responsibility for developing an ‘urban’ programme. There were few employees – most of the researchers – part-time academics as Fellows, some Research Fellows and PhD students – were due in October. I ran a workshop on ‘urban priorities’ and wondered what to do myself with no supporting resources. I was aware that my own research was on the fringes of Turing priorities – ‘data science’. I could claim to be a data scientist – and indeed Anthony Finkelstein, then a Trustee and a UCL colleague – in encouraging me to move to Turing said: “You can’t have ‘big data’ without big models”. However, in Turing, data science meant machine learning and AI rather than modelling as I practised it. So, I started to think about a new niche: Darwin in his later years decided to work on ‘smaller problems’, perhaps more manageable. I’m not comparing myself to Darwin, but there may be good advice there! And as for machine learning, though I put myself on a steep learning curve to learn something new and to fit in, though I couldn’t see how I could manage the ‘10,000 hours’ challenge that would turn me into a credible researcher in that field.

At the end of September, everything changed. In odd circumstances – to be described elsewhere – I found myself as the Institute CEO. There was suddenly a huge workload. I reported to a Board of Trustees, there were committees to work with, there were five partner universities to be visited. Above all, a new strategy had to be put in place – hewed out of a mass of ideas and forcefully-stated disagreements. Unsurprisingly, this blog was put on hold. I can now begin to record what I learned about a new field of research (for me) and the challenges of setting up a new Institute. I had to learn enough about data science and AI to be able to give presentations about the Institute and its priorities to a wide variety of audiences. I was able to attend seminars and workshops and talk to a great variety of people and by a process of osmosis, I began to make progress. I will start by recording some of my own experiences of collaboration in the Institute.

The ideal of collaboration is crucial for a national institute. Researchers from different universities, from industry, from the public sector, meet in workshops and seminars, and perhaps above all over coffee and lunch in our kitchen area, and new projects, new collaborations emerge. I can offer three examples from early days from my own experience which have enabled me to keep my own research alive in unexpected ways. (There are later ones which I will return to in due course.)

I met Weisi Guo at the August 2016 ‘urban priorities’ workshop. He presented his work on the analysis of global networks connecting cities which demonstrated the probabilities of conflicts. Needless to say, this turned out to be of interest to the Ministry of Defence and through the Institute’s partnership in this area, a project to develop this work was funded by DSTL. It seemed to me that Weisi’s work could be enhanced by adding flows (spatial interaction) and structural dynamics and we have worked together on this since our first meeting. New collaborators have been brought in and we have published a number of papers. From each of our viewpoints, adding research from a different previously unknown field, has proved highly fruitful.

The second example took me into the field oh health. Mihaela van der Schaar arrived at Turing in October from UCLA, to a Chair in Oxford and as a Turing Fellow. One of her fields of research is the application of machine learning to rapid and precise medical diagnosis. This is complex territory involving the accounting of co-morbidities as contributing to the diagnosis and prognosis of any particular disease, and having an impact on treatment plans. I recognised this as important for the Institute and was happy to support it. We had a lucky break early on. I was giving a breakfast briefing to a group of Chairs and CEOs of major companies and at the end of the meeting, I was approached by Caroline Cartellieri who thanked me for the presentation but said she wanted to talk to me about something else: she was a Trustee of the Cystic Fibrosis Trust. This led to Mihaela and her teams – mainly of PhD students – carrying out a project for the Trust which became an important demonstration of what could be achieved more widely – as well as being valuable for the Trust’s own clinicians. For me, it opened up the idea of incorporating the diagnosis and prognosis methods into a ‘learning machine’ which could ultimately be the basis of personalised medicine. And then a further thought: the health learning machine is generic: it can be applied to any flow of people for which there is a possible intervention to achieve an objective. For example, it can be applied to the flow of offenders into and out of prisons and this idea is now being developed in a project with the Ministry of Justice.

 Mihaela’s methods have also sown the seed of a new approach to urban modelling. The data for the co-morbidities’ analysis is the record over time of the occurrence of earlier diseases. If these events are re-interpreted in the urban modelling context as ‘life events’ -from demographics – birth migration and death – but to include entry to education, new job, new house and so on, then a new set of tools can be brought to bear.

The third example, still from very early on, probably Autumn 2016, came from me attending for my own education a seminar by Mark Girolami on (I think) the propagation of uncertainty – something I have never been any good at building into urban models. However, I recognised intuitively that his methods seemed to include a piece of mathematics that would possibly solve a problem that has always defeated me: how to predict the distribution of (say) retail centre sizes in a dynamic model. I discussed this with Mark who enthusiastically agreed to offer the problem to a (then) new research student, Louis Ellam. He also brought in an Imperial College colleague, Greg Pavliotis, an expert in statistical mechanics and therefore connected to my style of modelling. Over the next couple of years, the problem was solved and led to a four-author paper in Proceedings A of the Royal Society, with Louis as the first author.

Collaboration in Turing now takes place on a large scale. For me, it has taken me into fruitful new areas, my collaborators making it both manageable for me and adding new skills – thereby solving the ’10,000 hours’ challenge!

Alan Wilson

June 2019

44. Competing models? Deconstruct into building bricks?

Models are representations of theories. I write this as a modeller – someone who works on mathematical and computer models of cities and regions but who is also seriously interested in the underlying theories I am trying to represent. My field, relative say to physics, is underdeveloped. This means that we have a number of competing models and it is interesting to explore the basis of this and how to respond. There may be implications for other fields – even physics!

A starting conjecture is that there are two classes of competing models: (i) those that represent different underlying theories (or hypotheses); and (ii) those that stem from the modellers choosing different ways of making approximations in seeking to represent very complex systems. The two categories overlap of course. I will conjecture at the outset that most of the differences lie in the second (perhaps with one notable exception). So let’s get the first out of the way. Economists want individuals to maximise utility and firms to maximise profits – simplifying somewhat of course. They can probably find something that public services can maximise – health outcomes, exam results – indeed a whole range of performance indicators. There is now a recognition that for all sorts of reasons, the agents do not behave perfectly and way have been found to handle this. There is a whole host of (usually) micro-scale economic and social theory that is inadequately incorporated into models, in some cases because of the complexity issue – the niceties are approximated away; but in principle, that can be handled and should be. There is a broader principle lurking here: for most modelling purposes, the underlying theory can be seen as maximising or minimising something. So if we are uncomfortable with utility functions or economics more broadly, we can still try to represent behaviour in these terms – if only to have a base line from which behaviour deviates.

So what is the exception – another kind of dividing line which should perhaps have been a third category? At the pure end of a spectrum, ‘letting the data speak for themselves’. It is mathematics vs statistics; or econometrics vs mathematical economics. Statistical models look very different – at least at first sight – to mathematical models – and usually demand quite stringent conditions to be in place for their legitimate application. Perhaps, in the quantification of a field of study, statistical modelling comes first, followed by the mathematical? Of course there is a limit in which both ‘pictures’ can merge: many mathematical models, including the ones I work with, can be presented as maximum likelihood models. This is a thread that is not to be pursued further here, and I will focus on my own field on mathematical modelling.

There is perhaps a second high-level issue. It is sometimes argued that there are two kinds of mathematician: those that think in terms of algebra and those who think in terms of geometry. (I am in the algebra category which I am sure biases my approach.) As with many of these dichotomies, they should be removed and both perspectives fully integrated. But this is easier said than done!

How do the ‘approximations’ come about? I once tried to estimate the number of variables I would like to have for a comprehensive model of a city of 1M people and at a relatively coarse grain, the answer was around 1013! This demonstrates the need for approximation. The first steps can be categorised in terms of scale: first, spatial – referenced by zones of location rather than continuous space – and how large should the zones be? Second, temporal: continuous time or discrete? Third, sectoral: how many characteristics of individuals or organisations should be identified and at how fine a grain? Experience suggests that the use of discrete zones – and indeed other discrete definitions – makes the mathematics much easier to handle. Economists often use continuous space in their models, for example, and this forces them into another kind of approximation: monocentricity, which is hopelessly unrealistic. Many different models are simply based on different decisions about, and representations of, scale.

The second set of differences turn on focus of interest. One way of approximating is to consider a subsystem such as transport and the journey to work, or retail and the flow of revenues into a store or a shopping centre. The dangers here are the critical interdependencies are lost and this always has to be borne in mind. Consider the evaluation of new transport infrastructure for example. If this is based purely on a transport model, there is a danger than the cost-benefit analysis will be concentrated on time savings rather than the wider benefits. There is also a potentially higher-level view of focus. Lowry very perceptively once pointed out that models often focus on activities – and the distribution of activities across zones; or on the zones, in which case the focus would be on land use mix in a particular area. The trick, of course, is to capture both perspectives simultaneously – which is what Lowry achieved himself very elegantly but which has been achieved only rarely since.

A major bifurcation in model design turns on the time dimension and the related assumptions about dynamics. Models are much easier to handle if it is possible to make an assumption that the system being modelled is either in equilibrium or will return to a state of equilibrium quickly after a disturbance. There are many situations where the equilibrium assumption is pretty reasonable – for representing a cross-section in time or for short-run forecasting, for example, representing the way in which a transport system returns to equilibrium after a new network link or mode is introduced. But the big challenge is in the ‘slow dynamics’: modelling how cities evolve.

It is beyond the scope of this piece to review a wide range of examples. If there is a general lesson here it is that we should be tolerant of each others’ models, and we should be prepared to deconstruct them to facilitate comparison and perhaps to remove what appears to be competition but needn’t be. The deconstructed elements can then be seen as building bricks that can be assembled in a variety of ways. For example, ‘generalised cost’ in an entropy-maximising spatial interaction model can easily be interpreted as a utility function and therefore not in competition with economic models. Cellular automata models, and agent-based models are similarly based on different ‘pictures’ – different ways of making approximations. There are usually different strengths and weaknesses in the different alternatives. In many cases, with some effort, they can be integrated. From a mathematical point of view, deconstruction can offer new insights. We have, in effect, argued that model design involves making a series of decisions about scale, focus, theory, method and so on. What will emerge from this kind of thinking is that different kinds of representations – ‘pictures’ – have different sets of mathematical tools available for the model building. And some of these are easier to use than others, and so, when this is made explicit, might guide the decision process.

Alan Wilson

August 2016

43. Lowering the bar

A few weeks ago, I attended a British Academy workshop on ‘Urban Futures’ – partly focused on research priorities and partly on research that would be useful for policy makers. The group consisted mainly of academics who were keen to discuss the most difficult research challenges. I found myself sitting next to Richard Sennett – a pleasure and a privilege in itself, someone I’d read and knew by repute but whom I had never met. When the discussion turned to research contributions to policy, Richard made a remark which resonated strongly with me and made the day very much worthwhile. He said: “If you want to have an impact on policy, you have to lower the bar!” We discussed this briefly at the end of the meeting, and I hope he won’t mind if I try to unpick it a little. It doesn’t tell the whole story of the challenge of engaging the academic community in policy, but it does offer some insights.

The most advanced research is likely to be incomplete and to have many associated uncertainties when translated into practice. This can offer insights, but the uncertainties are often uncomfortable for policy makers. If we lower the bar to something like ‘best practice’ – see preceding blog 42 – this may involve writing and presentations which do not offer the highest levels of esteem in the academic community. What is on offer to policy makers has to be intelligible, convincing and useful. Being convincing means that what we are describing should evidence-based. And, of course, when these criteria are met, there should be another kind of esteem associated with the ‘research for policy’ agenda. I guess this is what ‘impact’ is supposed to be about (though I think that is half of the story, since impact that transforms a discipline may be more important in the long run).

‘Research for policy’ is, of course, ‘applied research’ which also brings up the esteem argument: if ‘applied’, then less ‘esteemful’ if I can make up a word. In my own experience, engagement with real challenges – whether commercial or public – adds seriously to basic research in two ways: first, it throws up new problems; and secondly, it provides access to data – for testing and further model development – that simply wouldn’t be available otherwise. Some of the new problems may be more challenging and in a scientific sense more important, than the old ones.

So, back to the old problem: what can we do to enhance academic participation in policy development? First a warning: recall the policy-design-analysis argument much used in these blogs. Policy is about what we are trying to achieve, design is about inventing solutions; and analysis is about exploring the consequences of, and evaluating, alternative policies, solutions and plans – the point being that analysis alone, the stuff of academic life, will not of itself solve problems. Engagement, therefore, ideally means engagement across all three areas, not just analysis.

How can we then make ourselves more effective by lowering the bar? First, ensure that our ‘best practice’ (see blog 42) is intelligible, convincing and useful; evidence-based. This means being confident about what we know and can offer. But then we also ought to be open about what we don’t know. In some cases we may be able to say that we can tackle, perhaps reasonably quickly, some of the important ‘not known’ questions through research; and that may need resource. Let me illustrate this with retail modelling. We can be pretty confident about estimating revenues (or people) attracted to facilities when something changes – a new store, a new hospital or whatever. And then there is a category, in this case, of what we ‘half know’. We have an understanding of retail structural dynamics to a point where we can estimate the minimum size that a new development has to be for it to succeed. But we can’t yet do this with confidence. So a talk on retail dynamics to commercial directors may be ‘above the bar’.

I suppose another way of putting this argument is that for policy engagement purposes, we should know where we should set the height of the bar: confidence below, uncertainty (possibly with some insights), above. There is a whole set of essays to be written on this for different possible application areas.

Alan Wilson

June 2016.

42. Best practice

Everything we do, or are responsible for, should aim at adopting ‘best practice’. This is easier said than done! We need knowledge, capability and capacity. Then maybe there are three categories through which we can seek best practice: (1) from ‘already in practice’ elsewhere; (2) could be in practice somewhere but isn’t: the research has been done but hasn’t been transferred; (3) problem identified, but research needed.

How do we acquire the knowledge? Through reading, networking, cpe courses, visits. Capability is about training, experience, acquiring skills. Capacity is about the availability of capability – access to it – for the services (let us say) that need it. Medicine provides an obvious example; local government another. How do each of 164 local authorities in England acquire best practice? Dissemination strategies are obviously important. We should also note that there may be central government responsibilities. We can expect markets to deliver skills, capabilities and capacities – through colleges, universities and, in a broad sense, industry itself (in its most refined way through ‘corporate universities’). But in many cases, there will be a market failure and government intervention becomes essential. In a field such as medicine, which is heavily regulated, the Government takes much of the responsibility for ensuring supply of capability and capacity. There are other fields, where in early stage development, consultants provide the capacity until it becomes mainstream – GMAP in relation to retailing being an example from my own experience. (See the two ‘spin-out blogs.)

How does all this work for cities, and in particular, for urban analytics? Good analytics provide a better base for decision making, planning and problem solving in city government. This needs a comprehensive information system which can be effectively interrogated. This can be topped with a high-level ‘dashboard’ with a hierarchy of rich underpinning levels. Warning lights might flash at the top to highlight problems lower down the hierarchy for further investigation. It needs a simulation (modelling) capacity for exploring the consequences of alternative plans. Neither of these needs are typically met. In some specific areas, it is potentially, and sometimes actually, OK: in transport planning in government; in network optimisation for retailers for example. A small number of consultants can and do provide skills and capability. But in general, these needs are not met, often not even recognised. This seems to be a good example of a market failure. There is central government funding and action – through research councils and particularly perhaps, Innovate UK. The ‘best practice’ material exists – so we are somewhere in between categories 1 and 2 of the introductory paragraph above. This tempts me to offer as a conjecture the obvious ‘solution’: what is needed are top-class demonstrators. If the benefits were evident, then dissemination mechanisms would follow!

Alan Wilson
June 2016

41 Foresight on The Future of Cities

For the last three years (almost), I have been chairing the Lead Expert Group of the Government Office for Science Foresight Project on The Future of Cities. It has finally ‘reported’, not as conventionally with one large report and many recommendations, but with four reports and a mass of supporting papers. We knew at the outset that we could not look forward without learning the lessons of the past, and so we commissioned a set of working papers – which are on the web site – as a resource, historical in the main, looking forwards imaginatively where possible. The ‘Foresight Future of Cities’ web site is at https://www.gov.uk/government/collections/future-of-cities.

During the project, we have worked with fourteen Government Department – ‘cities’ as a topic crosses government – and we have visited over 20 cities in the UK and have continued to work with a number of them. The project had several (sometimes implicit) objectives: to articulate the challenges facing cities from a long run – 50 years – perspective; to consider what could be done in the short run in evidence-based policy development to generate possibly better outcomes in meeting these challenges; to review what we know and what we don’t know – the latter implying that we can say something about research priorities; and to review the tools that are available to support foresight thinking.

We developed six themes that seemed to work for us throughout the project:

  • people – living in cities
  • city economies
  • urban metabolism – energy and materials flows and the sustainability agenda
  • urban form – including the issues associated with density and connectivity
  • infrastructure – including transport
  • governance – devolution and mayors?

What have we achieved? I believe we have a good conceptual framework and a corresponding effective understanding of the scale of the challenges. It is clear that to meet these challenges in the long term, radical thinking is needed to support future policy and planning development. The project has a science provenance and this provides the analytical base for exploring alternative future scenarios. Forecasting for the long term is impossible, inventing knowledge-based future scenarios is not. In our work with cities – Newcastle and Milton Keynes provide striking examples – we have been met with enthusiasm and local initiatives have produced high-class explorations, complete with effective public engagement. There is a link to the Newcastle report on the GO-Science website; the Milton Keynes work is ongoing.

Direct links to the four project reports follow. The first is an overview; the second a brief review of what we know about the science of cities combined with an articulation of research priorities; the third is, in effect, a foresighting manual for cities who wish to embark on this journey; and the fourth is an experiment – work on a particular topic – graduate mobility – since ‘skills’ figures prominently in our future challenges list.

An overview of the evidence


Science of Cities:


Foresight for Cities:


Graduate Mobility:


Alan Wilson

May 2016

40: Competing models

My immediately preceding blog post, ‘Truth is what we agree about’, provides a framework for thinking about competing models in the social sciences. There are competing models in physics, but not in relation to most of the ‘core’ – which is ‘agreed’. Most, probably all, of the social sciences are not as mature and so if we have competition, it is not surprising. However, it seems to me that we can make some progress by recognising that our systems of interest are typically highly complex and it is very difficult to isolate ideal and simple systems of interest (as physicists do) to develop the theory – even the building bricks. Much of the interest rests in the complexity. So that means that we have to make approximations in our model building. We can then distinguish two categories of competing models: those that are developed through the ‘approximations’ being done differently; and those that are paradigmatically different. Bear in mind also that models are representations of theories and so the first class – different ways of approximating – may well have the same underlying theory; whereas the second will have different theoretical underpinnings in at least some respects.

I can illustrate these ideas from my own experience. Much of my work has been concerned with spatial interaction: flows across space – for example, journey to work, to shop, to school, to health services, telecoms’ flows of all kinds. Flows decrease with ‘distance’ – measured as some kind of generalised cost – and increase with the attractiveness of the destination. There was even an early study that showed that marriage partners were much more likely to find each other if they lived or worked ‘nearer’ to each other – something that might be different now in times of greater mobility. Not surprisingly, these flows were first modelled on a Newtonian gravity model analogy. The models didn’t quite work and my own contribution was to shift from a Newtonian analogy to a Boltzmann one – a statistical averaging procedure. In this case, there is a methodological shift, but as in physics, whatever there is in underlying theory is the same: the physics of particles is broadly the same in Newton or Boltzmann. The difference is because Newton can deal with small numbers of particles, Boltzmann with very large numbers – but answering different questions. The same applies in spatial interaction: it is the large number methodology that works.

These models are consistent with an interpretation that people behave according to how they perceive ‘distance’ and ‘attractiveness’. Economists then argue that people behave so as to maximise utility functions. In this case the two can be linked by making the economists’ utility functions those that appear in the spatial interaction model. This is easily done – provided that it is recognised that the average behaviour is such that it does not arise from the maximisation of a particular utility function. So the economists have to assume imperfect information and/or, a variety of utility functions. They do this in most instances by assuming a distribution of such functions which, perhaps not surprisingly, is closely related to an entropy function. The point of this story is that apparently competing models can be wholly reconciled even though in some cases the practitioners on one side or other firmly locate themselves in silos that proclaim the rightness of their methods.

The same kind of system can be represented in an agent-based model – an ABM. In this case, the model functions with individuals who then behave according to rules. At first sight, this may seem fundamentally different but in practice, these rules are probabilities that can be derived from the coarser grain models. Indeed, this points us in a direction that shows how quite a range of models can be integrated. At the root of all the models I am using as an illustration, are conditional probabilities – a probability that an individual will make a particular trip from an origin to a destination. These probabilities can then be manipulated in different ways at different scales.

An argument is beginning to emerge that most of the differences involve judgements about such things as scale – of spatial units, sectors or temporal units – or methodology. The obvious example of the latter is the divide between statisticians and mathematicians, particularly as demonstrated by econometrics and mathematical economics. But, recall, we all work with probabilities, implicitly or explicitly.

There is perhaps one more dimension that we need to characterise differences in the social sciences when we are trying to categorise possibly competing approaches. That is when the task in hand is to ‘solve’ a real-world problem, or to meet a challenge. This determines some key variables at the outset: work on housing would need housing in some way as a variable and the corresponding data. This in turn illustrates a key aspect of the social scientists approach: the choice of variables to include in a model. We know that our systems are complex and the elements – the variables in the model – are highly interdependent. Typically, we can only handle a fraction of them, and when these choices are made in different ways for different purposes, it appears that we have competing models.  Back to approximations again.

Much food for thought. The concluding conjecture is that most of the differences between apparently competing models come from either different ways of making approximations, or  through different methodological (rather than theoretical) approaches. Below the surface, there are degrees of commonality that we should train ourselves to look for; and we should be purposeful!

Alan Wilson

May 2016

39: Abstract modes, generalised costs and constraints: exploring future scenarios

I have spent much of the last three years working on the Government Office for Science Foresight project on The future of cities. The focus was on a time horizon of fifty years into the future. It is clearly impossible to use urban models to forecast such long-term futures but it is possible in principle to explore systematically a variety of future scenarios. A key element of such scenarios is transport and we have to assume that what is on offer – in terms of modes of travel – will be very different to today – not least to meet sustainability criteria. The present dominance of car travel in many cities is likely to disappear. How, then, can we characterise possible future transport modes?

This takes me back to ideas that emerged in papers published 50 years ago (or in one case, almost that). In 1966 Dick Quandt and William Baumol, distinguished Princeton economists, published a paper in the Journal of Regional Science on ‘abstract transport modes’. Their argument was precisely that in the future, technological change would produce new modes: how could they be modelled? Their answer was to say that models should be calibrated not with modal parameters, but with parameters that related to the characteristics of modes. The calibrated results could then be used to model the take up of new modes that had new characteristics. By coincidence, Kelvin Lancaster, Columbia University economist, published a paper, also in 1966, in The Journal of Political Economy on ‘A new approach to consumer theory’ in which utility functions were defined in terms of the characteristics of goods rather than the goods themselves. He elaborated this in 1971 in his book ‘Consumer demand: a new approach’. In 1967, my ‘entropy’ paper was published in the journal Transportation Research and a concept used in this was that of ‘generalised cost’. This assumed that the cost of travelling by a mode was not just a money cost, but the weighted sum of different elements of (dis)utility: different kinds of time, comfort and so as well as money costs. The weights could be estimated as part of model calibration. David Boyce and Huw Williams in their magisterial history of transport modelling, ‘Forecasting urban travel’, wrote, quoting my 1967 paper, “impedance … may be measured as actual distance, as travel time, as cost, or more effectively as some weighted combination of such factors sometimes referred to as generalised cost……… In later publications, ‘impedance’ fell out of use in favour of ‘generalised cost’”. (They kindly attributed the introduction of ‘generalised cost’ to me.)

This all starts to come together. The Quandt and Baumol ‘abstract mode’ idea has always been in my mind and I was attracted to the Kelvin Lancaster argument for the same reasons – though that doesn’t seem to have taken off in a big way in economics. (I still have his 1971 book, purchased from Austicks in Leeds for £4-25.) I never quite connected ‘generalised cost’ to ‘abstract modes’. However, I certainly do now. When we have to look ahead to long-term future scenarios, it is potentially valuable to envisage new transport modes in generalised cost terms. By comparing one new mode with another, we can make an attempt – approximately because we are transporting current calibrated weights fifty years forward – to estimate the take up of modes by comparing generalised costs. I have not yet seen any systematic attempt to explore scenarios in this way and I think there is some straightforward work to be done – do-able in an undergraduate or master’s thesis!

We can also look at the broader questions of scenario development. Suppose for example, we want to explore the consequences of high density development around public transport hubs. These kinds of policies can be represented in our comprehensive models by constraints – and I argue that the idea of representing policies – or more broadly ‘knowledge’ – in constraints within models is another powerful tool. This also has its origins in a fifty year old paper – Jack Lowry’s ‘Model of metropolis’. In broad terms, this represents the fixing through plans of a model’s exogenous variables – but the idea of ‘constraints’ implies that there are circumstances where we might want to fix what we usually take as endogenous variables.

So we have the machinery for testing and evaluating long-term scenarios – albeit building on fifty year old ideas. It needs a combination of imagination – thinking what the future might look like – and analytical capabilities – ‘big modelling’. It’s all still to play for, but there are some interesting papers waiting to be written!!

Alan Wilson

April 2016

38. Truth is what we agree about?

I have always been interested in philosophy. I was interested in the big problems – the ‘What is life about?’ kind of thing with, as a special subject, ‘What is truth?’. How can we know whether something – a sentence, a theory, a mathematical formula – is true? And I guess because I was a mathematician and a physicist early in my career, I was particularly interested in the subset of this which is the philosophy of mathematics and the philosophy of science. I read a lot of Bertrand Russell – which perhaps seems rather quaint now. This had one nearer contemporary consequence. I was at the first meeting of the Vice-Chancellors of universities that became the Russell Group. There was a big argument about the name. We were meeting in the Russell Hotel and after much time had passed, I said something like ‘Why not call it the Russell Group?’ – citing not just the hotel but also Bertrand Russell as a mark of intellectual respectability. Such is the way that brands are born.

The maths and the science took me into Popper and the broader reaches of logical positivism. Time passed and I found myself a young university professor, working on mathematical models of cities, then the height of fashion. But fashions change and by the late 70s, on the back of distinguished works like David Harvey’s ‘Social justice and the city’, I found myself under sustained attack from a broadly Marxist front. ‘Positivism’ became a term of abuse and Marxism, in philosophical terms – or at least my then understanding of it, merged into the wider realms of structuralism. I was happy to come to understand that there were hidden (often power) structures to be revealed in social research that the models I was working on missed, therefore undermining the results.

This was serious stuff. I could reject some of the attacks in a straightforward way. There was a time when it was argued that anything mathematical was positivist and therefore bad and/or wrong. This could be rejected on the grounds that mathematics was a tool and that indeed there were distinguished Marxist mathematical economists such as Sraffa. But I had to dig deeper in order to understand. I read Marx, I read a lot of structuralists some of whom, at the time, were taking over English departments. I even gave a seminar in the Leeds English Department on structuralism!

In my reading, I stumbled on Jurgen Habermas and this provided a revelation for me. It took me back to questions about truth and provided a new way of answering them. In what follows, I am sure I oversimplify. His work is very rich in ideas, but I took a simple idea from it: truth is what we agree about. I say this to students now who are usually pretty shocked. But let’s unpick it. We can agree that 2 + 2 = 4. We can agree about the laws of physics – up to a point anyway – there are discoveries to be made that will refine these laws as has happened in the past. That also connects to another idea that I found useful in my toolkit: C. S. Peirce and the pragmatists. I will settle for the colloquial use of ‘pragmatism’: we can agree in a pragmatic sense that physics is true – and handle the refinements later. I would argue from my own experience that some social science is ‘true’ in the same way: much demography is true up to quite small errors – think of what actuaries do. But when we get to politics, we disagree. We are in a different ball park. We can still explore and seek to analyse and having the Habermas distinction in place helps us to understand arguments.

How does the ‘agreement’ come about? The technical term used by Habermas is ‘intersubjective communication’ and there has to be enough of it. In other words, the ‘agreement’ comes on the back of much discussion, debate and experiment. This fits very well with how science works. A sign of disagreement is when we hear that someone has an ‘opinion’ about an issue. This should be the signal for further exploration, discussion and debate rather than simply a ‘tennis match’ kind of argument.

Where does this leave us as social scientists? We are unlikely to have laws in the same way that physicists have laws but we have truths, even if they are temporary and approximate. We should recognise that research is a constant exploration in a context of mutual tolerance – our version of intersubjective communication. We should be suspicious of the newspaper article which begins ‘research shows that …..’ when the ‘research’ quoted is a single sample survey. We have to tread a line between offering knowledge and truth on the one hand and recognising the uncertainty of our offerings on the other. This is not easy in an environment where policy makers want to know what the evidence is, or what the ‘solution’ is, for pressing problems and would like to be more assertive than we might feel comfortable with. The nuances of language to be deployed in our reporting of research become critical.

Alan Wilson

April 2016

37: The ‘Leicester City’ phenomenon: aspirations in academia.

Followers of English football will be aware that the top tier is the Premier League and that the clubs that finish in the top four at the end of the season play in the European Champions’ League in the following year. These top four places are normally filled by four of a top half a dozen or so clubs – let’s say Manchester United, Manchester City, Arsenal, Chelsea, Tottenham Hotspur and Liverpool. There are one or two others on the fringe. This group does not include Leicester City. At Christmas 2014, Leicester were bottom of the Premier League with relegation looking inevitable. They won seven of their last nine games in that season and survived. At the beginning of the current (2015-16) season, the bookmakers’ odds on them winning the Premier League were 5000-1 against. At the time of writing, they top the league by eight points with four matches to play. The small number of people who might have bet £10 or more on them last August are now sitting on a potential fortune.

How has this been achieved? They have a very strong defence and so concede little; they can score ‘on the break’, notably through Jamie Vardy, a centre forward who not long ago was playing for Fleetwood Town in the nether reaches of English football; they have a thoughtful, experienced and cultured manager in Claudio Ranieri; and they work as a team. It is certainly a phenomenon and the bulk of the football-following population would now like to see them win the League.

What are the academic equivalents? There are university league tables and it is not difficult to identify a top half dozen. There are tables for departments and subjects. There is a ranking of journals. I don’t think there is an official league table of research groups but certainly some informal ones. As in football, it is very difficult to break into the top group from a long way below. Money follows success – as in the REF (the Research Excellence Framework) – and facilitates the transfer of the top players to the top group. So what is the ‘Leicester City’ strategy for an aspiring university, an ambitious department or research group, or a journal editor? The strong defence must be about having the basics in place – good REF ratings and so on. The goal-scoring break-out attacks is about ambition and risk taking. The ‘manager’ can inspire and aspire. And the team work: we are almost certainly not as good as we should be in academia, so food for thought there.

Then maybe all of the above requires at the core – and I’m sure Leicester City have these qualities – hard work, confidence, and good plans while still being creative; and a preparedness to be different – not to follow the fashion. So when The Times Higher has its ever-expanding annual awards, maybe they should add a ‘Leicester City Award’ for the university that matches their achievement in our own leagues. Meanwhile, will Leicester win the League? Almost all football followers in the country are now on their side. We will see in a month’s time!

Alan Wilson, April 2016

36: Block chains and urban analytics

I argued in an earlier piece that game-changing advances in urban analytics may well depend on technological change. One such possibility is the introduction of block chain software. a block is a set of accounts at a node. This is part of a network of many nodes many of which – in some cases all? – are connected. Transactions are recorded in the appropriate nodal accounts with varying degrees of openness. It is this openness that guarantees veracity and verifiability. This technology is considered to be a game changer in the financial world – with potential job losses because a block chain system excludes the ‘middlemen’ who normally record the transactions. Illustrations of the concept on the internet almost all rely on the bitcoin technology as the key example.

The ideas of ‘accounts at nodes’ and ‘transactions between nodes’ resonate very strongly with the core elements of urban analytics and models – the location of activities and spatial interaction. In the bitcoin case, the nodes are presumably account holders but it is no stretch of the imagination to imagine the nodes as being associated with spatial addresses. There must also be a connection to the ‘big data’ agenda and the ‘internet of things’. Much of the newly available real time data is transactional and one can imagine it being transmitted to blocks and used to update data bases on a continuous basis. This would have a very obvious role in applied retail modelling for example.

If this proved to be a mechanism for handling urban and regional data, and because a block chain is not owned by anyone, this could be a parallel internet for our research community.

This is a shorter than usual blog piece because to develop the idea, I need to do a lot more work!! The core concepts are complicated and not easy to follow. I have watched two You Tube videos – an excellent one from the Kahn Academy. I recommend these but what I would really like is someone to take on the challenge of (a) really understanding block chains and (b) thinking through possible urban analytics applications!

Alan Wilson

April  2016

35 Big data and high-speed analytics

My first experience of big data and high-speed analytics was at CERN and the Rutherford Lab over 50 years ago. I was in the Rutherford Lab part of a large distributed team working on a CERN bubble chamber experiment. There was a proton-proton collision every second or so which, for the charged particles, produced curved tracks in the chamber which were photographed from three different angles. The data from these tracks was recorded in something called the Hough-Powell device (after its inventors) in real time. This data was then turned into geometry; this geometry was then passed to my program. I was at the end of the chain and my job was to take the geometry, work out for this collision which of a number of possible events it actually was – the so-called kinematics analysis. This was done by chi-squared testing which seemed remarkably effective. The statistics of many events could then be computed, hopefully leading to the discovery of new (and anticipated) particles – in our case the Ω. In principle, the whole process for each event, through to identification, could be done in real time – though in practice, my part was done off-line. It was in the early days of big computers, in our case, the IBM 7094. I suspect now it will be all done in real time. Interestingly, in a diary I kept at the time, I recorded my immediate boss, John Burren, as remarking that ‘we could do this for the economy you know’!

So if we could do it then for quite a complicated problem, why don’t we do it now? Even well-known and well-developed models – transport and retail for example – typically take weeks or even months to calibrate, usually from a data set that refers to a point in time. We are progressing to a position at which, for these models, we could have the data base continually updated from data flowing from censors. (There is an intermediate processing point of course: to convert the sensor data to what is needed for model calibration.) This should be a feasible research challenge. What would have to be done? I guess the first step would be to establish data protocols so by the time the real data reached the model – the analytics platform, it was in some standard form. The concept of a platform is critical here. This would enable the user to select the analytical toolkit needed for a particular application. This could incorporate a whole spectrum from maps and other visualisation to the most sophisticated models – static and dynamic.

There are two possible guiding principles for the development of this kind of system: what is needed for the advance of the science, and what is needed for urban planning and policy development. In either case, we would start from an analysis of ‘need’ and thus evaluate what is available from the big data shopping list for a particular set of purposes – probably quite a small subset. There is a lesson in this alone: to think what we need data for rather than taking the items on the shopping list and asking what we can use them for.

Where do we start? The data requirements of various analytics procedures are pretty well known. There will be additions – for example incorporating new kinds of interaction from the Internet-of-Things world. This will be further developed in the upcoming blog piece on block chains.

So why don’t we do all this now? Essentially because the starting point – the first demo – is a big team job, and no funding council has been able to tackle something on this scale. There lies a major challenge. As I once titled a newspaper article: ‘A CERN for the social sciences’?

Alan Wilson

March 2016

34. What would Warren Weaver say now?

Warren Weaver was a remarkable man. He was a distinguished mathematician and statistician. He made important early contributions on the possibility of the machine translation of languages. He was a fine writer who recognised the importance of Shannon’s work on communications and the measurement of information and he worked with Shannon to co-author ‘The mathematical theory of communication’. But perhaps above all, he was a highly significant science administrator. For almost 30 years, from 1932, he worked in senior positions for the Rockefeller Foundation, latterly as Vice-president. I guess he had quite a lot of money to spend. From his earliest days with the Foundation, he evolved a strategy which was potentially a game-changer, or at the very least, seriously prescient: he switched his funding priorities from the physical sciences to the biological. In 1948, he published a famous paper in The American Scientist that justified this – maybe with an element of post hoc rationalisation – on the basis of three types of problem (or three types of system – according to taste): simple, of disorganised complexity and of organised complexity. Simple systems have a relatively small number of entities; complex systems have a very large number. The entities in the systems of disorganised complexity interact only weakly; those of organised complexity have entities that interact strongly. In the broadest terms – my language not his – Newton had solved the problems of simple systems and Boltzmann those of disorganised complexity. The biggest research challenges, he argued, were those of systems of organised complexity and more of these were to be found in the biological sciences than the physical. How right he was and it has only been after some decades that ‘complexity science’ has come of age – and become fashionable. (I was happy to re-badge myself as a complexity scientist which may have helped me to secure a rather large research grant.)

There is famous management scientist, no longer alive, called Peter Drucker. Such was his fame that a book was published confronting various business challenges with the title: ‘What would Peter Drucker say now?’. Since to my knowledge, no one has updated Warren Weaver’s analysis, I am tempted to pose the question ‘What would Warren Weaver say now?’. I have used his analysis for some years to argue for more research on urban dynamics – recognising cities as systems of organised complexity. But let’s explore the harder question: given that we understand urban organised complexity – though we haven’t progressed a huge distance with the research challenge – if Warren Weaver was alive now and could invest in research on cities, could we imagine what he might say to us. What could the next game changer be? I will argue it for ‘cities’ but I suspect, mutatis mutandis, the argument could be developed for other fields. Let’s start by exploring where we stand against the original Weaver argument.

We can probably say a lot about the ‘simple’ dimension. Computer visualisation for example can generate detailed maps on demand which can provide excellent overviews of urban challenges. We have done pretty well on the systems of disorganised complexity in areas like transport, retail and beyond. This has been done in an explicit Boltzmann-like way with entropy maximising models but also with various alternatives – from random utility models via microsimulation to agent-based modelling (ABM). We have made a start on understanding the slow dynamics with a variety of differential and difference equations, some with roots in the Lotka-Volterra models, some connected to Turing’s model of morphogenesis. What kinds of marks would Weaver give us? Pretty good on the first two: making good use of dramatically increased computing power and associated software development. I think on the disorganised complexity systems, when he saw that we have competing models for representing the same system, he would tell us to get that sorted out: either decide which is best and/or work out the extent to which they are equivalent or not at some underlying level. He might add one big caveat: we have not applied this science systematically and we have missed opportunities to use it to help tackle major urban challenges. On urban dynamics and organised complexity, we would probably get marks for making a goodish start but with a recommendation to invest a lot more.

So we still have a lot to do – but where do we look for the game changers? Serious application of the science – equilibrium and dynamics – to the major urban challenges could be a game changer. A full development of the dynamics would open up the possibility of ‘genetic planning’ by analogy with ‘genetic medicine’. But for the really new, I think we have to look to rapidly evolving technology. I would single out two examples, and there may be many more. The first is in one sense already old hat: big data. However, I want to argue that if it can be combined with hi-speed analytics, this could be a game changer. The second is something which is entirely new to me and may not be well known in the urban sciences: block chains. A block is some kind of set of accounts at a node. A block chain is made up of linked nodes – a network. There is much more to it and it is being presented as a disruptive technology that will transform the financial world (with many job losses?). If you google it, you will find out that it is almost wholly illustrated by the bitcoin system. A challenge is to work out how it could transform urban analytics and planning.

I have left serious loose ends which I won’t be able to tie up but which I will begin to elaborate the challenges with four further blog posts in coming weeks: (1) Competing models; (2) Big data and hi-speed analytics; (3) Block chains in urban analysis; (4) Applying the science to urban challenges.

Alan Wilson

March 2016

33: On writing

Research has to be ‘written up’. To some, writing comes easily – though I suspect this is on the basis of learning through experience. To many, especially research students at the time of thesis writing, it seems like a mountain to be climbed. There are difficulties of getting started, there are difficulties of keeping going! An overheard conversation in the Centre where I work was reported to me by a third party: “Why don’t you try Alan’s 500 words a day routine?” The advice I had been giving to one student – not a party to this conversation – was obviously being passed around. So let’s try that as a starting point. 500 words doesn’t feel mountainous. If you write 500 words a day, 5 days a week, 4 weeks a month, 10 months a year, you will write 100,000 words: a thesis, or a long book, or a shorter book and four papers. It is the routine of writing that achieves this so the next question is: how to achieve this routine? This arithmetic, of course, refers to the finished product and this needs preparation. In particular, it needs a good and detailed outline. If this can be achieved, it also avoids the argument that ‘I can only write if I have a whole day or a whole week’: the 500 words can be written in an hour or two first thing in the morning, it can be sketched on a train journey. In other words, in bits of time rather than the large chunks that are never available in practice.

The next questions beyond establishing a routine are: what to write and how to write? On the first, content is key: you must have something interesting to say; on the second what is most important is clarity of expression, which is actually clarity of thought. How you do it is for your own voice and that, combined with clarity, will produce your own style. I can offer one tip on how to achieve clarity of expression: become a journal editor. I was very lucky that early in my career I became first Assistant Editor of Transportation Research (later TR B) and then Editor of Environment and Planning (later EP A). As an editor you often find yourself in a position of thinking ‘There is a really good idea here but the writing is awful – it doesn’t come through’. This can send you back to the author with suggestions for rewriting, though in extreme cases, if the paper is important, you do the rewriting yourself. This process made me realise that my own writing was far from the first rank and I began to edit it as though I was a journal editor. I improved. So the moral can perhaps be stated more broadly: read your own writing as through an editor’s eyes – the editor asking ‘What is this person trying to say?’.

The content, in my experience, accumulates over time and there are aids to this. First, always carry a notebook! Second, always have a scratch pad next to you as you write to jot down additional ideas that have to be squeezed in. The ‘how to’ is then a matter of having a good structure. What are the important headings? There may be a need for a cultural shift here. Writing at school is about writing essays and it is often the case that a basic principle is laid down which states: ‘no headings’. I guess this is meant to support good writing so that the structure of the essay and the meaning can be conveyed without headings. I think this is nonsense – though if, say a magazine demands this, then you can delete the headings before submission! This is a battle I am always prepared to fight. In the days when I had tutorial groups, I always encouraged the use of headings. One group refused point blank to do this on the basis of their school principle. I did some homework and for the following week, I brought in a book of George Orwell’s essays, many of which had headings. I argued that if George Orwell could do it, so could everybody, and I more or less won.

The headings are the basis of the outline of what is to be written. I would now go further and argue that clarity, especially in academic writing, demands subheadings and sub-subheadings – a hierarchy in fact. This is now reinforced by the common use of Powerpoint for presentations. This is a form of structured writing and Powerpoint bullets, with sequences of indents, are hierarchical – so we are now all more likely to be brought up with this way of thinking. Indeed, I once had a sequence of around 200 Powerpoint slides for a lecture course. I produced a short book by using this as my outline. I converted the slides to Word, and then I converted the now bullet-less text to prose.

I am a big fan of numbered and hierarchical outlines: 1, 1.1, 1.1.1, 1.1.2, 1.2,…..2, 2.1, 2.1.1, 2.1.2, etc. This is an incredibly powerful tool. At the top level are say 6 main headings, then maybe six subheadings and so on. The structure will change as the writing evolves – a main heading disappears and another one appears. This is so powerful, I became curious about who invented it and resorted to google. There is no clear answer, and indeed it says something about the contemporary age that most of the references offer advice on how to use this system in Microsoft Word! However, I suspect the origins are probably in Dewey’s Library classification system – still in use – in effect a classification of knowledge. Google ‘Dewey’s decimal classification’ to find its Nineteenth Century history.

There are refinements to be offered on the ‘What to ….’ and ‘How to ….’ questions. What genre: an academic paper, a book – a text book? – a paper intended to influence policy, written for politicians or civil servants? In part, this can be formulated as ‘be clear about your audience’. One academic audience can be assumed to be familiar with your technical language; another may be one that you are trying to draw into an interdisciplinary project and might need more explanation. A policy audience probably has no interest in the technicalities but would like to be assured that they are receiving real ‘evidence’.

What next? Start writing, experiment; above all, always have something on the go – a chapter, a paper or a blog piece. Jot down new outlines in that notebook. As Mr Selfridge said, ‘There’s no fun like work!’ Think of writing as fun. It can be very rewarding – when it’s finished!!

Alan Wilson

December 2015

32: DNA

The idea of ‘DNA’ has become a commonplace metaphor. The real DNA is the genetic code that underpins the development of organisms. I find the idea useful in thinking about the development of – the evolution of – cities. This development depends very obviously on ‘what is there already’ – in technical terms, we can think of that as the ‘initial conditions’ for the next stage. We can then make an important distinction between what can change quickly – the pattern of a journey to work for instance – and what changes only slowly – the pattern of buildings or a road network. It is the slowly changing stuff that represents urban DNA. Again, in technical terms, it is the difference between the fast dynamics and the slow dynamics. The distinction is between the underlying structure and the activities that can be carried out on that structure.

It also connects to the complexity science picture of urban evolution and particularly the idea of path dependence. How a system evolves depends on the initial conditions. Path dependence is a series of initial conditions. We can then add that if there are nonlinear relations involved – scale economies for example – then the theory shows us the likelihood of phase changes – abrupt changes in structure. The evolution of supermarkets is one example of this; gentrification is another.

This offers another insight: future development is constrained by the initial conditions. We can therefore ask the question: what futures are possible – given plans and investment – from a given starting point? This is particularly important if we want to steer the system of interest towards a desirable outcome, or away from an undesirable one – also, a tricky one this, taking account of possible phase changes. This then raises the possibility that we can change the DNA: we can invest in such a way as to generate new development paths. This would be the planning equivalent of genetic medicine – ‘genetic planning’. There is a related and important discovery from examining retail dynamics from this perspective. Suppose there is a planned investment in a new retail centre at a particular location. This constitutes an addition to the DNA. The dynamics then shows that this investment has to exceed a certain critical size for it to succeed. If this calculation could be done for real-life examples (as distinct from proof-of-concept research explorations) then this would be incredibly valuable in planning contexts. Intuition suggests that a real life example might be the initial investment in Canary Wharf in London: that proved big enough in the end to pull with it a tremendous amount of further investment. The same thing may be happening with the Cross Rail investment in London – around stations such as Farringdon.

The ‘structure vs activities’ distinction may be important in other contexts as well. It has always seemed to me in a management context that it is worth distinguishing between ‘maintenance’ and ‘development’, and keeping these separate – that is, between keeping the organisation running as it is, and planning the investment that will shape its future.

The DNA idea can be part of our intuitive intellectual toolkit, and can then function more formally and technically in dynamic modelling. The core insight is worth having!!

Alan Wilson

December 2015

31: Too many journals, too many conferences?

Journals and conferences are certainly proliferating. I receive e-mails weekly inviting me to submit papers to new journals and daily inviting me to sign up for conferences. These are virtually all related to commercial profit-making enterprises rather than from, say, learned societies. (Though some learned societies make a large slice of their income from journals.) Inevitably this leads to a pecking order of journals which are long-established and those with high impact factors being important and supporting the idea of being a ‘top’ journal. I have some experience, of long ago, of being part of launching new journals, both from commercial publishers. I was the Assistant Editor of Transportation Research when it was first published in 1967 and Editor of Environment and Planning for its launch in 1969. They have grown, clearly being successful in their markets and meeting a demand. Transportation research now has Parts a, b, c, d and f and Environment and Planning has A, B, C and D. The 1969 volume of E and P had 2 issues, the 1970 volume, 4. Even E and P A now has 12 issue per annual volume. These are each journals which cover a broad field. Perhaps many of the new competitors are more niche oriented, perhaps not. Many of the long-established and prestigious journals continue to grow through addition of specialist marques – notably Nature for instance. Part of the growth is fuelled by the opportunities for on-line journals, and then related to this, to offering open access – something which is now required by research councils for example. The former offers low entry costs for the publisher and the latter a business model for which the author pays rather than the subscriber – though there may still be print editions.

Are there too many journals? At best, the current landscape is confusing for academic contributors. The new journals have to be filled and notwithstanding peer review, it must be tempting to publish papers which are not adding much to the corpus of knowledge. Indeed, a test of this is the very high proportion of published papers that end up with zero or maybe one citation. And where do editors find the army of referees that are needed? Of course, one reason for the increase is the growth of universities and the corresponding growth in academic staff. Most of these want to publish – for both good reasons and also – still good I guess – as a basis for promotion. So perhaps the number of journals matches this growth, and perhaps the pool of potential referees grows proportionately. Intuition suggests otherwise, but this would make a good research project for information scientists. Maybe it has been done?

This is still not answering the question: are there too many? In one sense, perhaps not – if this number of opportunities is necessary to support the publishing ambitions of the research community. But this leaves the problem of sorting out the real value but perhaps crowd sourcing solves this: some papers will rise to the top of the pile via citation counts. I thought when I started writing this piece that the answer to the question that I pose for myself would be that there are too many – but now I feel more neutral. Perhaps the market should be left to sort things out. We don’t have any other option in practice anyway!!

But what about conferences? Learned Society conferences of long-standing provide promotional opportunities, especially for early-career staff. There are problems: the societies need fee-paying attendees and most staff can only claim expenses if they can say that they have had a paper accepted for a conference. This leads to huge numbers of papers and many parallel sessions, so that even in large conferences, the attendance in a parallel session may be in single figures. And of course, the primary function of conferences is probably ‘networking’ – so even when there are many parallel sessions in play, the coffee shops and bars will be full of truants chatting! Conference organisers might be advised to allocate more time for this rather than cramming the programme.

So again, we probably have to say: let the market sort things out – but with some riders – some things could be improved. a colleague of mine banned her young researchers from presenting papers at conferences that had already been presented at previous conferences. Perhaps conference organisers could take up the policies of many journal editors by asking for confirmation that a paper has not been previously presented or published. But of course there would be ways of steering round that. The big quality test for a conference – beyond the location, the networking and the facilities – should be: what is being announced that is really new. The final confirmation of the Higgs boson for example!

Alan Wilson

December 2015

30: Sledgehammers for wicked problems

There are many definitions of ‘wicked problems’ – first characterised by Rittel and Webber in the 1970s – try googling to explore. However, essentially, they are problems that are well known, difficult and that governments of all colours have attempted to solve. My own list, relating to cities in the UK, would be something like:

  • social
    • social disparities
    • welfare – unemployment, pensions,……
    • housing
  • services
    • health services – elements of post-code lottery, poor performance, resources
    • education – a long tail of poor performance – for individuals and schools
    • prisons – high levels of recidivism
  • economics
    • productivity outside the Greater South East
    • ‘poor’ towns – seaside towns for example
  • global, with local impacts – sustainability
    • responding to the globalisation of the economy
    • responding to climate change
    • food security
    • energy security
    • indeed security in general

There are lots of ways of doing this and much more detail could be added. See for example the book edited by Charles Clarke titled The too difficult box.

Even at this broad level of presentation, the issues all connect and this is one of the arguments, continually put, for joined-up government. It is almost certainly the case, for example, that the social list has to be tackled through the education system. Stating this, however, is insufficient. Children from deprived families arrive at school relatively ill-prepared – in terms of vocabulary for example and so start – it has been estimated – two years ‘behind’ and in a conventional system, there is a good chance that they never catch up. There are extremes of this. Children who have been in care for example rarely progress to higher education; and it then turns out that quite a high percentage of the prison population have at some stage in their lives been in care. Something fundamental is wrong there.

We can conjecture that there is another chain of causal links associated with housing issues. Consider not the overall numbers issue – that as a country we build 100,000 houses a year when the ‘need’ is estimated at 200,000 or more – but the fact that there are areas of very poor housing, usually associated with deprived families. I would argue that this is not a housing problem but an income problem – not enough resource for the families to maintain the housing. It is an income problem because it is an employment problem. It is an employment problem because it is a skills problem. It is a skills problem because it is an education problem. Hence the root, as implied earlier, lies in education. So a first step in seeking to tackle the issues on the list of to identify the causal chain and to begin with the roots.

What, then, is the ‘sledgehammer’ argument? If the problem can be articulated and analysed, then it should be possible to see ‘what can be done about it’. The investigation of feasibility then kicks in of course: solutions are usually expensive. However, we don’t usually manage to do the cost-benefit analysis at a broad scale. If we could be more effective in providing education for children in care, and for the rehabilitation of prisoners, expensive schemes could be paid for by savings in the welfare and prison budgets: invest to save.

Let’s start with education. There are some successful schools in potentially deprived areas – so examples are available. (This may not pick up the child care issues but we return to that later.) There are many studies that say that the critical factor in education is the quality of the teachers – so enhancing the status of the teaching profession and building on schemes such as Teach First will be very important. Much is being done, not quite enough. Above all, there must be a way of not accepting ‘failure’ in any individual cases. With contemporary technology, tracking is surely feasible, though the follow-up might involve lots of 1-1 work and that is expensive. Finally, there is a legacy issue: those from earlier cohorts who have been failed by the system will be part of the current welfare and unemployment challenge, and so again some kind of tracking, some joining up of social services, employment services and education, should provide strong incentives to engage in life-long learning programmes – serious catch up. The tracking and joining up part of this programme should also deal with children in care as a special case, and a component of the legacy programme should come to grips with the prison education and rehabilitation agenda. There is then an important add-on: it may be necessary for the state to provide employment in some cases. Consider people released from prison as one case. They are potentially unattractive to employers (though some are creative in this respect) and so employment through let’s say a Remploy type of scheme – maybe as a licence condition of (early?) release becomes a partial solution. This might help to take the UK back down the league table of prison population per capita. This could all in principle be done and paid for out of savings – though there may be an element of no pain ‘no gain’ at the start. There are examples where it is being done: let’s see how they could be scaled up.

Similar analyses could be brought to bear on other issues. Housing is at the moment driven by builders’ and developers’ business models; and as with teacher supply, there is a capacity issue. As we have noted, in part it needs to be driven by education, employment and welfare reforms as a contribution to affordability challenges. And it needs to be driven by planners who can switch from a development control agenda to a place-making one.

The rest of the list, for now, is, very unfairly, left as an exercise for the reader!! In all cases, radical thinking is required, but realistic solutions are available!! We can offer a Michael Barber check list for tackling problems – from his book How to run a government so that citizens benefit and taxpayers don’t go crazy – very delivery-focused, as is his wont. For a problem:

  • What are you trying to do?
  • How are you going to do it?
  • How do you know you will be on track?
  • if not on track, what will you do?

All good advice!

Alan Wilson

29: Universities in the not-too-distant future

Will universities look different in 25 or 50 years’ time? I think at least some will, perhaps all. There will be new imperatives for successful countries and regions, and universities can play a crucial role. It is commonplace to say that future societies and economies will be knowledge-based. The Swedish economist, Ake Andersson, used to argue that a successful region needed three Cs for success: creative, cognitive and communications capabilities. Universities are the heart of this provision. Continue reading “29: Universities in the not-too-distant future”

28: The brain as a model

An important part of my intellectual toolkit has been Stafford Beer’s book Brain of the firm, published in 1972. Stafford Beer was a larger than life character who was a major figure in operational research, cybernetics, general systems theory and management science. I have a soft spot for him because of his book and work more widely and because, though I never met him, he wrote to me in 1970 after the publication of my Entropy book saying that it was the best description of ‘entropy’ he had ever read. Continue reading “28: The brain as a model”

27: Beware of optimisation

The idea of ‘optimisation’ is basic to lots of things we do and to how we think. When driving from A to B, what is the optimum route? When we learn calculus for the first time, we quickly come to grips with the maximisation and minimisation of functions. This is professionalised within operational research. If you own a transport business, you have to plan a daily schedule of collections and deliveries. Continue reading “27: Beware of optimisation”

26: Time Management

When I was Chair of AHRC, I occasionally attended small meetings of academics who we were consulting about various issues – our version of focus groups. On one occasion, we were expecting comments – even complaints – about various AHRC procedures. What we actually heard were strong complaints about the participant’s universities who ‘didn’t allow them enough time to do research’. This was a function, of course, of the range of demands in contemporary academic life with at least four areas of work: teaching, research, administration and outreach – all figuring in promotion criteria. Continue reading “26: Time Management”

25: Spinning Out 2

Why spin out? There are a number of possible motivations ranging from money – supplementing income, for self and/or department – to the more altruistic – offering people or organisations outside the university something valuable to them. Possibly both. This means that you have something to offer of value and that someone else recognises this. There is a complicated interaction to be worked through at the outset – connecting some research or expertise to an external need or potential demand. Continue reading “25: Spinning Out 2”

24: Spinning Out 1

I estimate that once every two years for the last 20 or 30 years, there has been a report of an inquiry into the transfer of university research into the economy – for commercial or public benefits. The fact that the sequence continues demonstrates that this remains a challenge. One mechanism is the spinning out of companies from universities and this piece is in two parts – the first describing my own experience and the second seeking to draw some broader conclusions. Either part might offer some clues for budding entrepreneurs. Continue reading “24: Spinning Out 1”

23: Missing Data

All the talk of ‘big data’ sometimes carries the implication that we must now surely have all the data that we need. However, frequently, crucial data is ‘missing’. This can then be seen as inhibiting research: ‘can’t work on that because there’s no data’! For important research, I want to make the case that missing data can often be estimated with reasonable results. This then links to the ‘statistics vs mathematical models’ issue: purist statisticians really do need the data – or at least a good sample; if there is a good model, then there is a better chance of getting good estimates of missing data. Continue reading “23: Missing Data”

22: Requisite Knowledge

W Ross Ashby was a psychiatrist who, through books such as Design for a brain, was one of the pioneers of the development of systems theory (qv) in the 1950s. A particular branch of systems theory was ‘cybernetics’ – from the Greek ‘steering’ – essentially the theory of the ‘control’ of systems. This was, and I assume is, very much a part of systems engineering and it attracted mathematicians such as Norbert Weiner. For me, an enduring contribution was ‘Ashby’s Law of Requisite Variety’ which is simple in concept and anticipates much of what we now call complexity science. ‘Variety’ is a measure of the complexity of a system and is formally defined as the number of possible ‘states’ of a system of interest. A coin to be tossed has two possible states – heads or tails; a machine can have billions. Continue reading “22: Requisite Knowledge”

21: Research Priorities: A modeller’s perspective

(From the Urban transformations website)

We know a lot about cities, but there is much more that we need to know to meet future challenges effectively. My aim here is to sketch some research priorities from the perspective of the Government Office for Science Foresight Project on The Future of Cities  – but much coloured by a personal position of having spent 50 years of my life on a quest to build a comprehensive mathematical model of a city that is both good science and is useful for planning and policy purposes! This narrows what I can offer but I can argue that a combination of the Foresight framework and a modelling perspective provides a good starting point. Continue reading “21: Research Priorities: A modeller’s perspective”

20: Back to the future – Bradford trams

This is the twentieth blog in this weekly series and after this there will be a summer break – a restart in October all being well!

Trams have a long history in British cities and are now being re-invented for a contemporary context. Electric trams started in Bradford in 1892 and ran until 1951. I was brought up in Bradford in the 1940s and so the trams were an early experience for me. There weren’t many cars at that time either. Continue reading “20: Back to the future – Bradford trams”

19: Territories and flows

Territories are defined by boundaries at scales ranging from countries and indeed alliances of countries) to neighbourhoods via regions and cities. These may be government or administrative boundaries, some formal, some less so; or they may be socially defined as in gang territories in cities. Much data relates to territories; some policies are defined by them – catchment areas of schools or health facilities for example. It is at this point that we start to see difficulties. Continue reading “19: Territories and flows”

18: Against oblivion

I was at school in the 1950s – Queen Elizabeth Grammar School Darlington – with Ian Hamilton. He went on to Oxford and became a significant and distinguished poet, critic, writer and editor – notable, perhaps, for shunning academia and running his editorial affairs from the Pillar of Hercules in Greek Street in Soho. I can probably claim to be the first publisher of his poetry as Editor of the School Magazine – poems that, to my knowledge, have never been ‘properly’ published. We lost touch after school. He went on to national service and Oxford; I deferred national service and went to Cambridge. Continue reading “18: Against oblivion”

17: Equations with names: the importance of Lotka and Volterra (and Tolstoy?)

The most famous equations with names – in one case by universal association – seem to come from physics: Newton’s Law of Gravity – the gravitational force between two objects is proportional to their masses and inversely proportional to the distance between them; Maxwell’s equations for electromagnetic fields; the Navier-Stokes’ equation in fluid dynamics; and E = mc2, Einstein’s equation which converts mass into energy. Continue reading “17: Equations with names: the importance of Lotka and Volterra (and Tolstoy?)”

16: New maths needed

In the modern era, mathematical and computer models of cities have been in development for around sixty years – not surprisingly, mirroring the growth of computing power. Much has been achieved. We are pretty good at modelling the flows of people in cities for a variety of purposes and loading these trips on to transport networks; we are pretty good at estimating some activity totals at locations such as retail revenue or demand for housing. Much of this has been stitched together into comprehensive models, embracing demography and input-output economics. Continue reading “16: New maths needed”

15: Venturing into other disciplines

Urban and regional science – a discipline or a subdiscipline, or is it still called interdisciplinary? – has been good at welcoming people from other disciplines, notably in recent times, physicists. Can we venture outside our box? It would be rather good if we could make some good contributions to physics!! However, given that the problems we handle are in some sense generic – spatial interaction and so on Continue reading “15: Venturing into other disciplines”

14: Learning from history

I was recruited to a post that was the start of my urban modelling career in the Autumn of 1964 by Christopher Foster (now Sir Christopher) to work on the cost-benefit analysis of major transport projects. My job was to do the computing and mathematics and at the same time to learn some economics. Of course, the project needed good transport models and at the time, all the experience was in the United States. Christopher had worked with Michael Beesley (LSE) on the pioneering cost-benefit analysis of the Victoria Line. To move forward on modelling, in 1965, Christopher, Michael and I embarked on a tour of the US. Continue reading “14: Learning from history”

13: ‘Research on’ versus ‘research for’

Let us begin by asserting that any piece of research is concerned with a ‘system of interest’ – henceforth ‘the system’ (cf. Systems thinking). We can then make a distinction between the ‘science of the system’ and the ‘applied science relating to the system’. In the second case, the implication is that the system offers challenges and problems that the science (of that system or possibly also with ‘associated’ systems) might help with. In research terms, this distinction can be roughly classified as ‘research on’ the system and ‘research for’ the system. This might be physics on the one hand, and engineering on the other; or biological sciences and medicine. Continue reading “13: ‘Research on’ versus ‘research for’”

12: Excellence

I was Chair of the Arts and Humanities Research Council for 6 years up to December 2013. Like the other research councils, and like most universities, we always said that we funded research that is ‘excellent’ and ‘world class’. However, I was always troubled about how actually we defined and understood ‘excellence’ – both pre- and post-award – and justified our claims. In terms of citations of published papers, we could always say that we were second to the United States and that was some justification. Continue reading “12: Excellence”

11: Real challenges

One route into urban research 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. And we need to bear in mind the PDA framework (cf.’systems thinking’): policy, design, analysis. Good analysis will demonstrate the nature of the challenge; policy is usually to make progress with meeting it; 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, what is a sample of the issues? Let’s structure the argument in terms of half a dozen headings, and then take examples under each. Continue reading “11: Real challenges”

10: Adding depth: a ‘CERN’ for urban science

An appropriate ambition of the model-building component of urban science is the construction of the best possible comprehensive model which represents the interdependencies that make cities complex (and interesting) systems. To articulate this is to spell out a kind of research programme: how do we combine the best of what we know into such a general model? Most of the available ‘depth’ is in the application of particular submodels – notably transport and retail. If we seek to identify the ‘best’ – many subjective decisions here in a contested area – we define a large scale computing operation underpinned by a substantial information system that houses relevant data. Though a large task, this is feasible! How would we set about it?

The initial thinking through would be an iterative process. The first step would be to review all the submodels and in particular, their categorisation of their main variables – their system definitions. Almost certainly, these would not be consistent: each would have detail appropriate to that system. It would be necessary then – or would it? – to find a common set of definitions. Continue reading “10: Adding depth: a ‘CERN’ for urban science”

9: Combinatorial Evolution

Brian Arthur introduced a new and important idea in his book The nature of technology: that of ‘combinatorial evolution’. The argument, put perhaps overly briefly, is essentially this: a ‘technology’, an aeroplane say, can be thought of as a system, and then we see that it is made up of a number of subsystems; and these can be arranged in a hierarchy. Thus the plane has engines, engines have turbo blades etc. The control system must sit at a high level in the hierarchy and then at lower levels we will find computers. The key idea is that most innovation comes at lower levels in the hierarchy, and through combinations of these innovations – hence combinatorial evolution. The computer may have been invented to do calculations but, as with aeroplanes, now figures as the lynchpin of sophisticated control systems.

This provides a basis for exploring research priorities. Arthur is in the main concerned with hard technologies and with specifics, like aeroplanes. However, he does remark that the economy ‘is an expression of technologies’ and that technological change implies structural change. Then: ‘…economic theory does not usually enter [here]………. it is inhabited by historians’. We can learn something here about dynamics, about economics and about interdisciplinarity! Continue reading “9: Combinatorial Evolution”

8: Interdisciplinarity

Systems thinking (see earlier entry) drives us to interdisciplinarity: we need to know everything about a system of interest and that means anything and everything that any relevant discipline can contribute. For almost any social science system of interest, there will be available knowledge at least from economics, geography, history, sociology, politics plus enabling disciplines such as mathematics, statistics, computer science and philosophy; and many more. Even this statement points up the paucity of disciplinary approaches. We should recognise that the professional disciplines such as medicine already have a systems focus and so in one obvious sense are interdisciplinary. But in the medicine case, the demand for in-depth knowledge has generated a host of specialisms which again produce silos and a different kind of interdisciplinary challenge. Continue reading “8: Interdisciplinarity”

7: Following Fashion

Much research follows the current fashion. This leads me to develop an argument around two questions. How does ‘fashion’ come about? How should we respond to it? I begin by reflecting on my personal experience.

My research career began in transport modelling (cf. ‘Serendipity’ entry) in the 1960s and was driven forward from an academic perspective by my work on entropy maximising and from a policy perspective by working in a group of economists on cost-benefit analysis. Both modelling and cost-benefit analysis were the height of fashion at the time. Continue reading “7: Following Fashion”

6: How to start: some basic principles

There are starting points that we can take from ‘systems thinking’  and theory development (‘evolvere theoria et intellectum’). Add ‘methods’ (including data – ‘Nullius in verba’) to this and this becomes the STM first step.

  • S: define the system of interest, dealing with the various dimensions of scale etc
  • T: what kinds of theory, or understanding, can be brought to bear?
  • M: what kinds of methods are available to operationalise the theory, to build a model?

This is essentially analytical: how does the system of interest work? How has it evolved? What is its future? This approach will almost certainly force an interdisciplinary perspective and within that, force some choices. For example, statistics or mathematics? Econometrics or mathematical economics? We should also flag a connection to Brian Arthur’s (see ‘combinatorial evolution’ entry) ideas on the evolution of technology – applied to research. He would argue that our system of interest in practice can be broken down into a hierarchy of subsystems, and that innovation is likely to come from lower levels in the hierarchy. This was, in his case, technological innovation but it seems to me that this is applicable to research as well. Continue reading “6: How to start: some basic principles”

5: Evolvere theoria et intellectum

We need data; but we need to encapsulate our understanding of cities in theories; and then we need to represent these theories in models. From ‘Nullius in verba’ to ‘Evolvere theoria et intellectum’ as a subsidiary motto: develop theory and understanding.

Can we ever have theory in the way that physicists have theory? Of course not, in that we have too many uncertainties at the micro-scale – the behaviours of individuals and organisations and this creates uncertainties at broader scales. We can’t calculate ‘constants’ (parameters) to umpteen decimal places and our data points do not fit precisely onto smooth lines or curves. But if we ask the right questions, we can develop theories in relation to those questions and then, from a quantitative perspective – and there are others! – we might say that a typical error level (or measure of uncertainty – is around 10% say. This is much better than not having the theory, particularly if it enables us to predict, at least for the short run. Continue reading “5: Evolvere theoria et intellectum”

4: Nullius in verba

‘Nullius in verba’ is the motto of the Royal Society. It can be roughly translated as ‘Don’t take anybody’s word for it’ with the implication, ‘verify through experiments’. Urban researchers – and social scientists more broadly – live in their laboratory and the data is created minute by minute. Our experiments are the interpretations of that data and the testing of theories and models – models as representations of theories. In the case of models, data is used for calibration and there has to be enough ‘left over’ for testing; or the calibrated model can be tested against a full, usually future, data set. We now live in an age of ‘big data’: the ‘minute by minute’ can be taken literally. Continue reading “4: Nullius in verba”

3: Lowry and his legacy

A brief history

The ‘science of cities’ has a long history. The city was the market for von Thunen’s analysis of agriculture in the late 18th Century. There were many largely qualitative explorations in the first half of the 20th Century. However, cities are complex systems and the major opportunities for scientific development came with the beginnings of computer power in the 1950s. This coincided with major investment in highways in the United States and computer models were developed to predict both current transport patterns and the impacts of new highways. Plans could be evaluated and the formal methods of what became cost-benefit analysis were developed around that time. However, it was always recognised that transport and land use were interdependent and that a more comprehensive model was needed. There were several attempts to build such models but the one that stands out is I. S. (Jack) Lowry’s model of Pittsburgh which was published in 1964. This was elegant and (deceptively) simple – represented in just 12 algebraic equations and inequalities. Many contemporary models are richer in detail and have many more equations but most are Lowry-like in that they have a recognisably similar core structure.[1] Continue reading “3: Lowry and his legacy”

2: Serendipity

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? Continue reading “2: Serendipity”

1: Systems Thinking

When I was studying physics, I was introduced to the idea of ‘system of interest’: defining at the outset that ‘thing’ you were immediately interested in learning about. There are three ideas to be developed from this starting point. First, it is important simply to list all the components of the system, what Graham Chapman called ‘entitation’; secondly, to simplify as far as possible by excluding all possible extraneous elements from this list; and thirdly, taking us beyond what the physicists were thinking at the time, to recognise the idea of a ‘system’ as made up of related elements, and so it was 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. Around the time that I was learning about the physicists’ ideas of a ‘system’, something more general, ‘systems theory’ was in the air though I didn’t become aware of it until much later. Continue reading “1: Systems Thinking”