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The Systematic Comparison of Agent-Based Policy Models – It’s time we got our act together!

By Mike Bithell and Bruce Edmonds

Model Intercomparison

The recent Covid crisis has led to a surge of new model development and a renewed interest in the use of models as policy tools. While this is in some senses welcome, the sudden appearance of many new models presents a problem in terms of their assessment, the appropriateness of their application and reconciling any differences in outcome. Even if they appear similar, their underlying assumptions may differ, their initial data might not be the same, policy options may be applied in different ways, stochastic effects explored to a varying extent, and model outputs presented in any number of different forms. As a result, it can be unclear what aspects of variations in output between models are results of mechanistic, parameter or data differences. Any comparison between models is made tricky by differences in experimental design and selection of output measures.

If we wish to do better, we suggest that a more formal approach to making comparisons between models would be helpful. However, it appears that this is not commonly undertaken most fields in a systematic and persistent way, except for the field of climate change, and closely related fields such as pollution transport or economic impact modelling (although efforts are underway to extend such systematic comparison to ecosystem models –  Wei et al., 2014, Tittensor et al., 2018⁠). Examining the way in which this is done for climate models may therefore prove instructive.

Model Intercomparison Projects (MIP) in the Climate Community

Formal intercomparison of atmospheric models goes back at least to 1989 (Gates et al., 1999)⁠ with the first atmospheric model inter-comparison project (AMIP), initiated by the World Climate Research Programme. By 1999 this had contributions from all significant atmospheric modelling groups, providing standardised time-series of over 30 model variables for one particular historical decade of simulation, with a standard experimental setup. Comparisons of model mean values with available data helped to reveal overall model strengths and weaknesses: no single model was best at simulation of all aspects of the atmosphere, with accuracy varying greatly between simulations. The model outputs also formed a reference base for further inter-comparison experiments including targets for model improvement and reduction of systematic errors, as well as a starting point for improved experimental design, software and data management standards and protocols for communication and model intercomparison. This led to AMIPII and, subsequently, to a series of Climate model inter-comparison projects (CMIP) beginning with CMIP I in 1996. The latest iteration (CMIP 6) is a collection of 23 separate model intercomparison experiments covering atmosphere, ocean, land surface, geo-engineering, and the paleoclimate. This collection is aimed at the upcoming 2021 IPCC process (AR6). Participating projects go through an endorsement process for inclusion, (a process agreed with modelling groups), based on 10 criteria designed to ensure some degree of coherence between the various models – a further 18 MIPS are also listed as currently active (https://www.wcrp-climate.org/wgcm-cmip/wgcm-cmip6). Groups contribute to a central set of common experiments covering the period 1850 to the near-present. An overview of the whole process can be found in (Eyring et al., 2016).

The current structure includes a set of three overarching questions covering the dynamics of the earth system, model systematic biases and understanding possible future change under uncertainty. Individual MIPS may build on this to address one or more of a set of 7 “grand science challenges” associated with the climate. Modelling groups agree to provide outputs in a standard form, obtained from a specified set of experiments under the same design, and to provide standardised documentation to go with their models. Originally (up to CMIP 5), outputs were then added to a central public repository for further analysis, however the output grew so large under CMIP6 that now the data is held dispersed over repositories maintained by separate groups.

Other Examples

Two further more recent examples of collective model  development may also be helpful to consider.

Firstly, an informal network collating models across more than 50 research groups has already been generated as a result of the COVID crisis –  the Covid Forecast Hub (https://covid19forecasthub.org). This is run by a small number of research groups collaborating with the US Centre for Disease Control and is strongly focussed on the epidemiology. Participants are encouraged to submit weekly forecasts, and these are integrated into a data repository and can be vizualized on the website – viewers can look at forward projections, along with associated confidence intervals and model evaluation scores, including those for an ensemble of all models. The focus on forecasts in this case arises out of the strong policy drivers for the current crisis, but the main point is that it is possible to immediately view measures of model performance and to compare the different model types: one clear message that rapidly becomes apparent is that many of the forward projections have 95% (and at some times, even 50%) confidence intervals for incident deaths that more than span the full range of the past historic data. The benefit of comparing many different models in this case is apparent, as many of the historic single-model projections diverge strongly from the data (and the models most in error are not consistently the same ones over time), although the ensemble mean tends to be better.

As a second example, one could consider the Psychological Science Accelerator (PSA: Moshontz et al 2018, https://psysciacc.org/). This is a collaborative network set up with the aim of addressing the “replication crisis” in psychology: many previously published results in psychology have proved problematic to replicate as a result of small or non-representative sampling or use of experimental designs that do not generalize well or have not been used consistently either within or across studies. The PSA seeks to ensure accumulation of reliable and generalizable evidence in psychological science, based on principles of inclusion, decentralization, openness, transparency and rigour. The existence of this network has, for example, enabled the reinvestigation of previous  experiments but with much larger and less nationally biased samples (e.g. Jones et al 2021).

The Benefits of the Intercomparison Exercises and Collaborative Model Building

More specifically, long-term intercomparison projects help to do the following.

  • Build on past effort. Rather than modellers re-inventing the wheel (or building a new framework) with each new model project, libraries of well-tested and documented models, with data archives, including code and experimental design, would allow researchers to more efficiently work on new problems, building on previous coding effort
  • Aid replication. Focussed long term intercomparison projects centred on model results with consistent standardised data formats would allow new versions of code to be quickly tested against historical archives to check whether expected results could be recovered and where differences might arise, particularly if different modelling languages were being used
  • Help to formalize. While informal code archives can help to illustrate the methods or theoretical foundations of a model, intercomparison projects help to understand which kinds of formal model might be good for particular applications, and which can be expected to produce helpful results for given desired output measures
  • Build credibility. A continuously updated set of model implementations and assessment of their areas of competence and lack thereof (as compared with available datasets) would help to demonstrate the usefulness (or otherwise) of ABM as a way to represent social systems
  • Influence Policy (where appropriate). Formal international policy organisations such as the IPCC or the more recently formed IPBES are effective partly through an underpinning of well tested and consistently updated models. As yet it is difficult to see whether such a body would be appropriate or effective for social systems, as we lack the background of demonstrable accumulated and well tested model results.

Lessons for ABM?

What might we be able to learn from the above, if we attempted to use a similar process to compare ABM policy models?

In the first place, the projects started small and grew over time: it would not be necessary, for example, to cover all possible ABM applications at the outset. On the other hand, the latest CMIP iterations include a wide range of different types of model covering many different aspects of the earth system, so that the breadth of possible model types need not be seen as a barrier.

Secondly, the climate inter-comparison project has been persistent for some 30 years – over this time many models have come and gone, but the history of inter-comparisons allows for an overview of how well these models have performed over time – data from the original AMIP I models is still available on request, supporting assessments concerning  long-term model improvement.

Thirdly, although climate models are complex – implementing a variety of different mechanisms in different ways – they can still be compared by use of standardised outputs, and at least some (although not necessarily all) have been capable of direct comparison with empirical data.

Finally, an agreed experimental design and public archive for documentation and output that is stable over time is needed; this needs to be done via a collective agreement among the modelling groups involved so as to ensure a long-term buy-in from the community as a whole, so that there is a consistent basis for long-term model development, building on past experience.

The need for aligning or reproducing ABMs has long been recognised within the community (Axtell et al. 1996; Edmonds & Hales 2003), but on a one-one basis for verifying the specification of models against their implementation, although (Hales et al. 2003) discusses a range of possibilities. However, this is far from a situation where many different models of basically the same phenomena are systematically compared – this would be a larger scale collaboration lasting over a longer time span.

The community has already established a standardised form of documentation in the ODD protocol. Sharing of model code is also becoming routine, and can be easily achieved through COMSES, Github or similar. The sharing of data in a long-term archive may require more investigation. As a starting project COVID-19 provides an ideal opportunity for setting up such a model inter-comparison project – multiple groups already have running examples, and a shared set of outputs and experiments should be straightforward to agree on. This would potentially form a basis for forward looking experiments designed to assist with possible future pandemic problems, and a basis on which to build further features into the existing disease-focussed modelling, such as the effects of economic, social and psychological issues.

Additional Challenges for ABMs of Social Phenomena

Nobody supposes that modelling social phenomena is going to have the same set of challenges that climate change models face. Some of the differences include:

  • The availability of good data. Social science is bedevilled by a paucity of the right kind of data. Although an increasing amount of relevant data is being produced, there are commercial, ethical and data protection barriers to accessing it and the data rarely concerns the same set of actors or events.
  • The understanding of micro-level behaviour. Whilst the micro-level understanding of our atmosphere is very well established, those of the behaviour of the most important actors (humans) is not. However, it may be that better data might partially substitute for a generic behavioural model of decision-making.
  • Agreement upon the goals of modelling. Although there will always be considerable variation in terms of what is wanted from a model of any particular social phenomena, a common core of agreed objectives will help focus any comparison and give confidence via ensembles of projections. Although the MIPs and Covid Forecast Hub are focussed on prediction, it may be that empirical explanation may be more important in other areas.
  • The available resources. ABM projects tend to be add-ons to larger endeavours and based around short-term grant funding. The funding for big ABM projects is yet to be established, not having the equivalent of weather forecasting to piggy-back on.
  • Persistence of modelling teams/projects. ABM tends to be quite short-term with each project developing a new model for a new project. This has made it hard to keep good modelling teams together.
  • Deep uncertainty. Whilst the set of possible factors and processes involved in a climate change model are well established, which social mechanisms need to be involved in any model of any particular social phenomena is unknown. For this reason, there is deep disagreement about the assumptions to be made in such models, as well as sharp divergence in outcome due to changes brought about by a particular mechanism but not included in a model. Whilst uncertainty in known mechanisms can be quantified, assessing the impact of those due to such deep uncertainty is much harder.
  • The sensitivity of the political context. Even in the case of Climate Change, where the assumptions made are relatively well understood and done on objective bases, the modelling exercise and its outcomes can be politically contested. In other areas, where the representation of people’s behaviour might be key to model outcomes, this will need even more care (Adoha & Edmonds 2017).

However, some of these problems were solved in the case of Climate Change as a result of the CMIP exercises and the reports they ultimately resulted in. Over time the development of the models also allowed for a broadening and updating of modelling goals, starting from a relatively narrow initial set of experiments. Ensuring the persistence of individual modelling teams is easier in the context of an internationally recognised comparison project, because resources may be easier to obtain, and there is a consistent central focus. The modelling projects became longer-term as individual researchers could establish a career doing just climate change modelling and importance of the work increasingly recognised. An ABM modelling comparison project might help solve some of these problems as the importance of its work is established.

Towards an Initial Proposal

The topic chosen for this project should be something where there: (a) is enough public interest to justify the effort, (b) there are a number of models with a similar purpose in mind being developed.  At the current stage, this suggests dynamic models of COVID spread, but there are other possibilities, including: transport models (where people go and who they meet) or criminological models (where and when crimes happen).

Whichever ensemble of models is focussed upon, these models should be compared on a core of standard, with the same:

  • Start and end dates (but not necessarily the same temporal granularity)
  • Covering the same set of regions or cases
  • Using the same population data (though possibly enhanced with extra data and maybe scaled population sizes)
  • With the same initial conditions in terms of the population
  • Outputting a core of agreed measures (but maybe others as well)
  • Checked against their agreement against a core set of cases, with agreed data sets
  • Reported on in a standard format (though with a discussion section for further/other observations)
  • well documented and with code that is open access
  • Run a minimum of times with different random seeds

Any modeller/team that had a suitable model and was willing to adhere to the rules would be welcome to participate (commercial, government or academic) and these teams would collectively decide the rules, development and write any reports on the comparisons. Other interested stakeholder groups could be involved including professional/academic associations, NGOs and government departments but in a consultative role providing wider critique – it is important that the terms and reports from the exercise be independent or any particular interest or authority.


We call upon those who think ABMs have the potential to usefully inform policy decisions to work together, in order that the transparency and rigour of our modelling matches our ambition. Whilst model comparison exercises of the kind described are important for any simulation work, particular care needs to be taken when the outcomes can affect people’s lives.


Aodha, L. & Edmonds, B. (2017) Some pitfalls to beware when applying models to issues of policy relevance. In Edmonds, B. & Meyer, R. (eds.) Simulating Social Complexity – a handbook, 2nd edition. Springer, 801-822. (A version is at http://cfpm.org/discussionpapers/236)

Axtell, R., Axelrod, R., Epstein, J. M., & Cohen, M. D. (1996). Aligning simulation models: A case study and results. Computational & Mathematical Organization Theory, 1(2), 123-141. https://link.springer.com/article/10.1007%2FBF01299065

Edmonds, B., & Hales, D. (2003). Replication, replication and replication: Some hard lessons from model alignment. Journal of Artificial Societies and Social Simulation, 6(4), 11. http://jasss.soc.surrey.ac.uk/6/4/11.html

Eyring, V., Bony, S., Meehl, G. A., Senior, C. A., Stevens, B., Stouffer, R. J., & Taylor, K. E. (2016). Overview of the Coupled Model Intercomparison Project Phase 6 (CMIP6) experimental design and organization. Geoscientific Model Development, 9(5), 1937–1958. https://doi.org/10.5194/gmd-9-1937-2016

Gates, W. L., Boyle, J. S., Covey, C., Dease, C. G., Doutriaux, C. M., Drach, R. S., Fiorino, M., Gleckler, P. J., Hnilo, J. J., Marlais, S. M., Phillips, T. J., Potter, G. L., Santer, B. D., Sperber, K. R., Taylor, K. E., & Williams, D. N. (1999). An Overview of the Results of the Atmospheric Model Intercomparison Project (AMIP I). In Bulletin of the American Meteorological Society (Vol. 80, Issue 1, pp. 29–55). American Meteorological Society. https://doi.org/10.1175/1520-0477(1999)080<0029:AOOTRO>2.0.CO;2

Hales, D., Rouchier, J., & Edmonds, B. (2003). Model-to-model analysis. Journal of Artificial Societies and Social Simulation, 6(4), 5. http://jasss.soc.surrey.ac.uk/6/4/5.html

Jones, B.C., DeBruine, L.M., Flake, J.K. et al. To which world regions does the valence–dominance model of social perception apply?. Nat Hum Behav 5, 159–169 (2021). https://doi.org/10.1038/s41562-020-01007-2

Moshontz, H. + 85 others (2018) The Psychological Science Accelerator: Advancing Psychology Through a Distributed Collaborative Network ,  1(4) 501-515. https://doi.org/10.1177/2515245918797607

Tittensor, D. P., Eddy, T. D., Lotze, H. K., Galbraith, E. D., Cheung, W., Barange, M., Blanchard, J. L., Bopp, L., Bryndum-Buchholz, A., Büchner, M., Bulman, C., Carozza, D. A., Christensen, V., Coll, M., Dunne, J. P., Fernandes, J. A., Fulton, E. A., Hobday, A. J., Huber, V., … Walker, N. D. (2018). A protocol for the intercomparison of marine fishery and ecosystem models: Fish-MIP v1.0. Geoscientific Model Development, 11(4), 1421–1442. https://doi.org/10.5194/gmd-11-1421-2018

Wei, Y., Liu, S., Huntzinger, D. N., Michalak, A. M., Viovy, N., Post, W. M., Schwalm, C. R., Schaefer, K., Jacobson, A. R., Lu, C., Tian, H., Ricciuto, D. M., Cook, R. B., Mao, J., & Shi, X. (2014). The north american carbon program multi-scale synthesis and terrestrial model intercomparison project – Part 2: Environmental driver data. Geoscientific Model Development, 7(6), 2875–2893. https://doi.org/10.5194/gmd-7-2875-2014

Bithell, M. and Edmonds, B. (2020) The Systematic Comparison of Agent-Based Policy Models - It’s time we got our act together!. Review of Artificial Societies and Social Simulation, 11th May 2021. https://rofasss.org/2021/05/11/SystComp/


Basic Modelling Hygiene – keep descriptions about models and what they model clearly distinct

By Bruce Edmonds

The essence of a model is that it relates to something else – what it models – even if this is only a vague or implicit mapping. Otherwise a model would be indistinguishable from any other computer code, set of equations etc (Hesse 1964; Wartofsky 1966). The centrality of this essence makes it unsurprising that many modellers seem to conflate the two.

This is made worse by three factors.

  1. A strong version of Kuhn’s “Spectacles” (Kuhn 1962) where the researcher goes beyond using the model as a way of thinking about the world to projecting their model onto the world, so they see the world only through that “lens”. This effect seems to be much stronger for simulation modelling due to the intimate interaction that occurs over a period of time between modellers and their model.
  2. It is a natural modelling heuristic to make the model more like what it models (Edmonds & al. 2019), introducing more elements of realism. This is especially strong with agent-based modelling which lends itself to complication and descriptive realism.
  3. It is advantageous to stress the potential connections between a model (however abstract) and possible application areas. It is common to start an academic paper with a description of a real-world issue to motivate the work being reported on; then (even if the work is entirely abstract and unvalidated) to suggest conclusions for what is observed. A lack of substantiated connections between model and any empirical data can be covered up by slick passing from the world to the model and back again and a lack of clarity as to what their research achieves (Edmonds & al. 2019).

Whatever the reasons the result is similar – that the language used to describe entities, processes and outcomes in the model is the same as that used for its descriptions of what is intended to be modelled.

Such conflation is common in academic papers (albeit to different degrees). Expert modellers will not usually be confused by such language because they understand the modelling process and know what to look for in a paper. Thus one might ask, what is the harm of a little rhetoric and hype in the reporting of models? After all, we want modellers to be motivated and should thus be tolerant of their enthusiasm. To show the danger I will thus look at an example that talks about modelling aspects of ethnocentrism.

In their paper, entitled “The Evolutionary Dominance of Ethnocentric Cooperation“, Hartshorn, Kaznatcheev & Shultz (2013) further analyse the model described in (Hammond & Axelrod 2006). The authors have reimplemented the original model and extensively analysed it especially the temporal dynamics. The paper is solely about the original model and its properties, there is no pretence of any validation or calibration with respect to any data. The problem is in the language used, because it the language could equally well refer to the model and the real world.

Take the first sentence of its abstract: “Recent agent-based computer simulations suggest that ethnocentrism, often thought to rely on complex social cognition and learning, may have arisen through biological evolution“. This sounds like the simulation suggests something about the world we live in – that, as the title suggests, Ethnocentric cooperation naturally dominates other strategies (e.g. humanitarianism) and so it is natural. The rest of the abstract then goes on in the same sort of language which could equally apply to the model and the real world.

Expert modellers will understand that they were talking about the purely abstract properties of the model, but this will not be clear to other readers. However, in this case there is evidence that it is a problem. This paper has, in recent years, shot to the top of page requests from the JASSS website (22nd May 2020) at 162,469 requests over a 7-day period, but is nowhere in the top 50 articles in terms of JASSS-JASSS citations. Tracing where these requests come from, results in many alt-right and Russian web sites. It seems that many on the far right see this paper as confirmation of their Nationalist and Racist viewpoints. This is far more attention than a technical paper just about a model would get, so presumably they took it as confirmation about real-world conclusions (or were using it to fool others about the scientific support for their viewpoints) – namely that Ethnocentrism does beat Humanitarianism and this is an evolutionary inevitability [note 1].

This is an extreme example of the confusion that occurs when non-expert modellers read many papers on modelling. Modellers too often imply a degree of real-world relevance when this is not justified by their research. They often imply real-world conclusions before any meaningful validation has been done. As agent-based simulation reaches a less specialised audience, this will become more important.

Some suggestions to avoid this kind of confusion:

  • After the motivation section, carefully outline what part this research will play in the broader programme – do not leave this implicit or imply a larger role than is justified
  • Add in the phrase “in the model” frequently in the text, even if this is a bit repetitive [note 2]
  • Keep  discussions about the real world in a different sections from those that discuss the model
  • Have an explicit statement of what the model can reliably say about the real world
  • Use different terms when referring to parts of the model and part of the real world (e.g. actors for real world individuals, agents in the model)
  • Be clear about the intended purpose of the model – what can be achieved as a result of this research (Edmonds et al. 2019) – for example, do not imply the model will be able to predict future real world properties until this has been demonstrated (de Matos Fernandes & Keijzer 2020)
  • Be very cautious in what you conclude from your model – make sure this is what has been already achieved rather than a reflection of your aspirations (in fact it might be better to not mention such hopes at all until they are realised)


  1. To see that this kind of conclusion is not necessary see (Hales & Edmonds 2019).
  2. This is similar to a campaign to add the words “in mice” in reports about medical “breakthroughs”, (https://www.statnews.com/2019/04/15/in-mice-twitter-account-hype-science-reporting)


Edmonds, B., et al. (2019) Different Modelling Purposes, Journal of Artificial Societies and Social Simulation 22(3), 6. <http://jasss.soc.surrey.ac.uk/22/3/6.html>. doi:10.18564/jasss.3993

Hammond, R. A., N. D. and Axelrod, R. (2006). The Evolution of Ethnocentrism. Journal of Conflict Resolution, 50(6), 926–936. doi:10.1177/0022002706293470

Hartshorn, Max, Kaznatcheev, Artem and Shultz, Thomas (2013) The Evolutionary Dominance of Ethnocentric Cooperation, Journal of Artificial Societies and Social Simulation 16(3), 7. <http://jasss.soc.surrey.ac.uk/16/3/7.html>. doi:10.18564/jasss.2176

Hesse, M. (1964). Analogy and confirmation theory. Philosophy of Science, 31(4), 319-327.

Kuhn, T. S. (1962). The Structure of Scientific Revolutions. Univ. of Chicago Press.

de Matos Fernandes, C. A. and Keijzer, M. A. (2020) No one can predict the future: More than a semantic dispute. Review of Artificial Societies and Social Simulation, 15th April 2020. https://rofasss.org/2020/04/15/no-one-can-predict-the-future/

Wartofsky, M. (1966). the Model Muddle – Proposals for an Immodest Realism. Journal Of Philosophy, 63(19), 589-589.

Edmonds, B. (2020) Basic Modelling Hygiene - keep descriptions about models and what they model clearly distinct. Review of Artificial Societies and Social Simulation, 22nd May 2020. https://rofasss.org/2020/05/22/modelling-hygiene/


What more is needed for Democratically Accountable Modelling?

By Bruce Edmonds

(A contribution to the: JASSS-Covid19-Thread)

In the context of the Covid19 outbreak, the (Squazzoni et al 2020) paper argued for the importance of making complex simulation models open (a call reiterated in Barton et al 2020) and that relevant data needs to be made available to modellers. These are important steps but, I argue, more is needed.

The Central Dilemma

The crux of the dilemma is as follows. Complex and urgent situations (such as the Covid19 pandemic) are beyond the human mind to encompass – there are just too many possible interactions and complexities. For this reason one needs complex models, to leverage some understanding of the situation as a guide for what to do. We can not directly understand the situation, but we can understand some of what a complex model tells us about the situation. The difficulty is that such models are, themselves, complex and difficult to understand. It is easy to deceive oneself using such a model. Professional modellers only just manage to get some understanding of such models (and then, usually, only with help and critique from many other modellers and having worked on it for some time: Edmonds 2020) – politicians and the public have no chance of doing so. Given this situation, any decision-makers or policy actors are in an invidious position – whether to trust what the expert modellers say if it contradicts their own judgement. They will be criticised either way if, in hindsight, that decision appears to have been wrong. Even if the advice supports their judgement there is the danger of giving false confidence.

What options does such a policy maker have? In authoritarian or secretive states there is no problem (for the policy makers) – they can listen to who they like (hiring or firing advisers until they get advice they are satisfied with), and then either claim credit if it turned out to be right or blame the advisers if it was not. However, such decisions are very often not value-free technocratic decisions, but ones that involve complex trade-offs that affect people’s lives. In these cases the democratic process is important for getting good (or at least accountable) decisions. However, democratic debate and scientific rigour often do not mix well [note 1].

A Cautionary Tale

As discussed in (Adoha & Edmonds 2019) Scientific modelling can make things worse, as in the case of the North Atlantic Cod Fisheries Collapse. In this case, the modellers became enmeshed within the standards and wishes of those managing the situation and ended up confirming their wishful thinking. An effect of technocratising the decision-making about how much it is safe to catch had the effect of narrowing down the debate to particular measurement and modelling processes (which turned out to be gravely mistaken). In doing so the modellers contributed to the collapse of the industry, with severe social and ecological consequences.

What to do?

How to best interface between scientific and policy processes is not clear, however some directions are becoming apparent.

  • That the process of developing and giving advice to policy actors should become more transparent, including who is giving advice and on what basis. In particular, any reservations or caveats that the experts add should be open to scrutiny so the line between advice (by the experts) and decision-making (by the politicians) is clearer.
  • That such experts are careful not to over-state or hype their own results. For example, implying that their model can predict (or forecast) the future of complex situations and so anticipate the effects of policy before implementation (de Matos Fernandes and Keijzer 2020). Often a reliable assessment of results only occurs after a period of academic scrutiny and debate.
  • Policy actors need to learn a little bit about modelling, in particular when and how modelling can be reliably used. This is discussed in (Government Office for Science 2018, Calder et al. 2018) which also includes a very useful checklist for policy actors who deal with modellers.
  • That the public learn some maturity about the uncertainties in scientific debate and conclusions. Preliminary results and critiques tend to be jumped on too early to support one side within polarised debate or models rejected simply on the grounds they are not 100% certain. We need to collectively develop ways of facing and living with uncertainty.
  • That the decision-making process is kept as open to input as possible. That the modelling (and its limitations) should not be used as an excuse to limit what the voices that are heard, or the debate to a purely technical one, excluding values (Aodha & Edmonds 2017).
  • That public funding bodies and journals should insist on researchers making their full code and documentation available to others for scrutiny, checking and further development (readers can help by signing the Open Modelling Foundation’s open letter and the campaign for Democratically Accountable Modelling’s manifesto).

Some Relevant Resources

  • CoMSeS.net — a collection of resources for computational model-based science, including a platform for publicly sharing simulation model code and documentation and forums for discussion of relevant issues (including one for covid19 models)
  • The Open Modelling Foundation — an international open science community that works to enable the next generation modelling of human and natural systems, including its standards and methodology.
  • The European Social Simulation Association — which is planning to launch some initiatives to encourage better modelling standards and facilitate access to data.
  • The Campaign for Democratic Modelling — which campaigns concerning the issues described in this article.


note1: As an example of this see accounts of the relationship between the UK scientific advisory committees and the Government in the Financial Times and BuzzFeed.


Barton et al. (2020) Call for transparency of COVID-19 models. Science, Vol. 368(6490), 482-483. doi:10.1126/science.abb8637

Aodha, L.Edmonds, B. (2017) Some pitfalls to beware when applying models to issues of policy relevance. In Edmonds, B. & Meyer, R. (eds.) Simulating Social Complexity – a handbook, 2nd edition. Springer, 801-822. (see also http://cfpm.org/discussionpapers/236)

Calder, M., Craig, C., Culley, D., de Cani, R., Donnelly, C.A., Douglas, R., Edmonds, B., Gascoigne, J., Gilbert, N. Hargrove, C., Hinds, D., Lane, D.C., Mitchell, D., Pavey, G., Robertson, D., Rosewell, B., Sherwin, S., Walport, M. & Wilson, A. (2018) Computational modelling for decision-making: where, why, what, who and how. Royal Society Open Science,

Edmonds, B. (2020) Good Modelling Takes a Lot of Time and Many Eyes. Review of Artificial Societies and Social Simulation, 13th April 2020. https://rofasss.org/2020/04/13/a-lot-of-time-and-many-eyes/

de Matos Fernandes, C. A. and Keijzer, M. A. (2020) No one can predict the future: More than a semantic dispute. Review of Artificial Societies and Social Simulation, 15th April 2020. https://rofasss.org/2020/04/15/no-one-can-predict-the-future/

Government Office for Science (2018) Computational Modelling: Technological Futures. https://www.gov.uk/government/publications/computational-modelling-blackett-review

Squazzoni, F., Polhill, J. G., Edmonds, B., Ahrweiler, P., Antosz, P., Scholz, G., Chappin, É., Borit, M., Verhagen, H., Giardini, F. and Gilbert, N. (2020) Computational Models That Matter During a Global Pandemic Outbreak: A Call to Action. Journal of Artificial Societies and Social Simulation, 23(2):10. <http://jasss.soc.surrey.ac.uk/23/2/10.html>. doi: 10.18564/jasss.4298

Edmonds, B. (2020) What more is needed for truly democratically accountable modelling? Review of Artificial Societies and Social Simulation, 2nd May 2020. https://rofasss.org/2020/05/02/democratically-accountable-modelling/


Good Modelling Takes a Lot of Time and Many Eyes

By Bruce Edmonds

(A contribution to the: JASSS-Covid19-Thread)

It is natural to want to help in a crisis (Squazzoni et al. 2020), but it is important to do something that is actually useful rather than just ‘adding to the noise’. Usefully modelling disease spread within complex societies is not easy to do – which essentially means there are two options:

  1. Model it in a fairly abstract manner to explore ideas and mechanisms, but without the empirical grounding and validation needed to reliably support policy making.
  2. Model it in an empirically testable manner with a view to answering some specific questions and possibly inform policy in a useful manner.

Which one does depends on the modelling purpose one has in mind (Edmonds et al. 2019). Both routes are legitimate as long as one is clear as to what it can and cannot do. The dangers come when there is confusion –  taking the first route whilst giving policy actors the impression one is doing the second risks deceiving people and giving false confidence (Edmonds & Adoha 2019, Elsenbroich & Badham 2020). Here I am only discussing the second, empirically ambitious route.

Some of the questions that policy-makers might want to ask, include, what might happen if we: close the urban parks, allow children of a specific range of ages go to school one day a week, cancel 75% of the intercity trains, allow people to go to beauty spots, visit sick relatives in hospital or test people as they recover and give them a certificate to allow them to go back to work?

To understand what might happen in these scenarios would require an agent-based model where agents made the kind of mundane, every-day decisions of where to go and who to meet, such that the patterns and outputs of the model were consistent with known data (possibly following the ‘Pattern-Oriented Modelling’ of Grimm & Railsback 2012). This is currently lacking. However this would require:

  1. A long-term, iterative development (Bithell 2018), with many cycles of model development followed by empirical comparison and data collection. This means that this kind of model might be more useful for the next epidemic rather than the current one.
  2. A collective approach rather than one based on individual modellers. In any very complex model it is impossible to understand it all – there are bound to be small errors and programmed mechanisms will subtly interaction with others. As (Siebers & Venkatesan 2020) pointed out this means collaborating with people from other disciplines (which always takes time to make work), but it also means an open approach where lots of modellers routinely inspect, replicate, pull apart, critique and play with other modellers’ work – without anyone getting upset or feeling criticised. This does involve an institutional and normative embedding of good modelling practice (as discussed in Squazzoni et al. 2020) but also requires a change in attitude – from individual to collective achievement.

Both are necessary if we are to build the modelling infrastructure that may allow us to model policy options for the next epidemic. We will need to start now if we are to be ready because it will not be easy.


Bithell, M. (2018) Continuous model development: a plea for persistent virtual worlds, Review of Artificial Societies and Social Simulation, 22nd August 2018. https://rofasss.org/2018/08/22/mb

Edmonds, B. & Adoha, L. (2019) Using agent-based simulation to inform policy – what could possibly go wrong? In Davidson, P. & Verhargen, H. (Eds.) (2019). Multi-Agent-Based Simulation XIX, 19th International Workshop, MABS 2018, Stockholm, Sweden, July 14, 2018, Revised Selected Papers. Lecture Notes in AI, 11463, Springer, pp. 1-16. DOI: 10.1007/978-3-030-22270-3_1

Edmonds, B., Le Page, C., Bithell, M., Chattoe-Brown, E., Grimm, V., Meyer, R., Montañola-Sales, C., Ormerod, P., Root, H., & Squazzoni, F. (2019). Different Modelling Purposes. Journal of Artificial Societies and Social Simulation, 22(3), 6. <http://jasss.soc.surrey.ac.uk/22/3/6.html> doi: 10.18564/jasss.3993

Elsenbroich, C. and Badham, J. (2020) Focussing on our Strengths. Review of Artificial Societies and Social Simulation, 12th April 2020. https://rofasss.org/2020/04/12/focussing-on-our-strengths/

Grimm, V., & Railsback, S. F. (2012). Pattern-oriented modelling: a ‘multi-scope’for predictive systems ecology. Philosophical Transactions of the Royal Society B: Biological Sciences, 367(1586), 298-310. doi:10.1098/rstb.2011.0180

Siebers, P-O. and Venkatesan, S. (2020) Get out of your silos and work together. Review of Artificial Societies and Social Simulation, 8th April 2020. https://rofasss.org/2020/0408/get-out-of-your-silos

Squazzoni, F., Polhill, J. G., Edmonds, B., Ahrweiler, P., Antosz, P., Scholz, G., Chappin, É., Borit, M., Verhagen, H., Giardini, F. and Gilbert, N. (2020) Computational Models That Matter During a Global Pandemic Outbreak: A Call to Action. Journal of Artificial Societies and Social Simulation, 23(2):10. <http://jasss.soc.surrey.ac.uk/23/2/10.html>. doi: 10.18564/jasss.4298

Edmonds, B. (2020) Good Modelling Takes a Lot of Time and Many Eyes. Review of Artificial Societies and Social Simulation, 13th April 2020. https://rofasss.org/2020/04/13/a-lot-of-time-and-many-eyes/


Predicting Social Systems – a Challenge

By Bruce Edmonds, Gary Polhill and David Hales

(Part of the Prediction-Thread)

There is a lot of pressure on social scientists to predict. Not only is an ability to predict implicit in all requests to assess or optimise policy options before they are tried, but prediction is also the “gold standard” of science. However, there is a debate among modellers of complex social systems about whether this is possible to any meaningful extent. In this context, the aim of this paper is to issue the following challenge:

Are there any documented examples of models that predict useful aspects of complex social systems?

To do this the paper will:

  1. define prediction in a way that corresponds to what a wider audience might expect of it
  2. give some illustrative examples of prediction and non-prediction
  3. request examples where the successful prediction of social systems is claimed
  4. and outline the aspects on which these examples will be analysed

About Prediction

We start by defining prediction, taken from (Edmonds et al. 2019). This is a pragmatic definition designed to encapsulate common sense usage – what a wider public (e.g. policy makers or grant givers) might reasonably expect from “a prediction”.

By ‘prediction’, we mean the ability to reliably anticipate well-defined aspects of data that is not currently known to a useful degree of accuracy via computations using the model.

Let us clarify the language in this.

  • It has to be reliable. That is, one can rely upon its prediction as one makes this – a model that predicts erratically and only occasionally predicts is no help, since one does not whether to believe any particular prediction. This usually means that (a) it has made successful predictions for several independent cases and (b) the conditions under which it works is (roughly) known.
  • What is predicted has to be unknown at the time of prediction. That is, the prediction has to be made before the prediction is verified. Predicting known data (as when a model is checked on out-of-sample data) is not sufficient [1]. Nor is the practice of looking for phenomena that is consistent with the results of a model, after they have been generated (due to ignoring all the phenomena that is not consistent with the model in this process).
  • What is being predicted is well defined. That is, How to use the model to make a prediction about observed data is clear. An abstract model that is very suggestive – appears to predict phenomena but in a vague and undefined manner but where one has to invent the mapping between model and data to make this work – may be useful as a way of thinking about phenomena, but this is different from empirical prediction.
  • Which aspects of data about being predicted is open. As Watts (2014) points out, this is not restricted to point numerical predictions of some measurable value but could be a wider pattern. Examples of this include: a probabilistic prediction, a range of values, a negative prediction (this will not happen), or a second-order characteristic (such as the shape of a distribution or a correlation between variables). What is important is that (a) this is a useful characteristic to predict and (b) that this can be checked by an independent actor. Thus, for example, when predicting a value, the accuracy of that prediction depends on its use.
  • The prediction has to use the model in an essential manner. Claiming to predict something obviously inevitable which does not use the model is insufficient – the model has to distinguish which of the possible outcomes is being predicted at the time.

Thus, prediction is different from other kinds of scientific/empirical uses, such as description and explanation (Edmonds et al. 2019). Some modellers use “prediction” to mean any output from a model, regardless of its relationship to any observation of what is being modelled [2]. Others use “prediction” for any empirical fitting of data, regardless of whether that data is known before hand. However here we wish to be clearer and avoid any “post-truth” softening of the meaning of the word for two reasons (a) distinguishing different kinds of model use is crucial in matters of model checking or validation and (b) these “softer” kinds of empirical purpose will simply confuse the wider public when if talk to themabout “prediction”. One suspects that modellers have accepted these other meanings because it then allows them to claim they can predict (Edmonds 2017).

Some Examples

Nate Silver and his team aim to predict future social phenomena, such as the results of elections and the outcome of sports competitions. He correctly predicted the outcomes of all 50 electoral colleges in Obama’s election before it happened. This is a data-hungry approach, which involves the long-term development of simulations that carefully see what can be inferred from the available data, with repeated trial and error. The forecasts are probabilistic and repeated many times. As well as making predictions, his unit tries to establish the level of uncertainty in those predictions – being honest about the probability of those predictions coming about given the likely levels of error and bias in the data. These models are not agent-based in nature but tend to be of a mostly statistical nature, thus it is debatable whether these are treated as complex systems – it certainly does not use any theory from complexity science. His book (Silver 2012) describes his approach. Post hoc analysis of predictions – explaining why it worked or not – is kept distinct from the predictive models themselves – this analysis may inform changes to the predictive model but is not then incorporated into the model. The analysis is thus kept independent of the predictive model so it can be an effective check.

Many models in economics and ecology claim to “predict” but on inspection, this only means there is a fit to some empirical data. For example, (Meese & Rogoff 1983) looked at 40 econometric models where they claimed they were predicting some time-series. However, 37 out of 40 models failed completely when tested on newly available data from the same time series that they claimed to predict. Clearly, although presented as being predictive models, they could not predict unknown data. Although we do not know for sure, presumably what happened was that these models had been (explicitly or implicitly) fitted to the out-of-sample data, because the out-of-sample data was already known to the modeller. That is, if the model failed to fit the out-of-sample data when the model was tested, it was then adjusted until it did work, or alternatively, only those models that fitted the out-of-sample data were published.

The Challenge

The challenge is envisioned as happening like this.

  1. We publicise this paper requesting that people send us example of prediction or near-prediction on complex social systems with pointers to the appropriate documentation.
  2. We collect these and analyse them according to the characteristics and questions described below.
  3. We will post some interim results in January 2020 [3], in order to prompt more examples and to stimulate discussion. The final deadline for examples is the end of March 2020.
  4. We will publish the list of all the examples sent to us on the web, and present our summary and conclusions at Social Simulation 2020 in Milan and have a discussion there about the nature and prospects for the prediction of complex social systems. Anyone who contributed an example will be invited to be a co-author if they wish to be so-named.

How suggestions will be judged

For each suggestion, a number of answers will be sought – namely to the following questions:

  • What are the papers or documents that describe the model?
  • Is there an explicit claim that the model can predict (as opposed to might in the future)?
  • What kind of characteristics are being predicted (number, probabilistic, range…)?
  • Is there evidence of a prediction being made before the prediction was verified?
  • Is there evidence of the model being used for a series of independent predictions?
  • Were any of the predictions verified by a team that is independent of the one that made the prediction?
  • Is there evidence of the same team or similar models making failed predictions?
  • To what extent did the model need extensive calibration/adjustment before the prediction?
  • What role does theory play (if any) in the model?
  • Are the conditions under which predictive ability claimed described?

Of course, negative answers to any of the above about a particular model does not mean that the model cannot predict. What we are assessing is the evidence that a model can predict something meaningful about complex social systems. (Silver 2012) describes the method by which they attempt prediction, but this method might be different from that described in most theory-based academic papers.

Possible Outcomes

This exercise might shed some light of some interesting questions, such as:

  • What kind of prediction of complex social systems has been attempted?
  • Are there any examples where the reliable prediction of complex social systems has been achieved?
  • Are there certain kinds of social phenomena which seem to more amenable to prediction than others?
  • Does aiming to predict with a model entail any difference in method than projects with other aims?
  • Are there any commonalities among the projects that achieve reliable prediction?
  • Is there anything we could (collectively) do that would encourage or document good prediction?

It might well be that whether prediction is achievable might depend on exactly what is meant by the word.


This paper resulted from a “lively discussion” after Gary’s (Polhill et al. 2019) talk about prediction at the Social Simulation conference in Mainz. Many thanks to all those who joined in this. Of course, prior to this we have had many discussions about prediction. These have included Gary’s previous attempt at a prediction competition (Polhill 2018) and Scott Moss’s arguments about prediction in economics (which has many parallels with the debate here).


[1] This is sufficient for other empirical purposes, such as explanation (Edmonds et al. 2019)

[2] Confusingly they sometimes the word “forecasting” for what we mean by predict here.

[3] Assuming we have any submitted examples to talk about


Edmonds, B. & Adoha, L. (2019) Using agent-based simulation to inform policy – what could possibly go wrong? In Davidson, P. & Verhargen, H. (Eds.) (2019). Multi-Agent-Based Simulation XIX, 19th International Workshop, MABS 2018, Stockholm, Sweden, July 14, 2018, Revised Selected Papers. Lecture Notes in AI, 11463, Springer, pp. 1-16. DOI: 10.1007/978-3-030-22270-3_1 (see also http://cfpm.org/discussionpapers/236)

Edmonds, B. (2017) The post-truth drift in social simulation. Social Simulation Conference (SSC2017), Dublin, Ireland. (http://cfpm.org/discussionpapers/195)

Edmonds, B., le Page, C., Bithell, M., Chattoe-Brown, E., Grimm, V., Meyer, R., Montañola-Sales, C., Ormerod, P., Root H. & Squazzoni. F. (2019) Different Modelling Purposes. Journal of Artificial Societies and Social Simulation, 22(3):6. http://jasss.soc.surrey.ac.uk/22/3/6.html.

Grimm V, Revilla E, Berger U, Jeltsch F, Mooij WM, Railsback SF, Thulke H-H, Weiner J, Wiegand T, DeAngelis DL (2005) Pattern-oriented modeling of agent-based complex systems: lessons from ecology. Science 310: 987-991.

Meese, R.A. & Rogoff, K. (1983) Empirical Exchange Rate models of the Seventies – do they fit out of sample? Journal of International Economics, 14:3-24.

Polhill, G. (2018) Why the social simulation community should tackle prediction, Review of Artificial Societies and Social Simulation, 6th August 2018. https://rofasss.org/2018/08/06/gp/

Polhill, G., Hare, H., Anzola, D., Bauermann, T., French, T., Post, H. and Salt, D. (2019) Using ABMs for prediction: Two thought experiments and a workshop. Social Simulation 2019, Mainz.

Silver, N. (2012). The signal and the noise: the art and science of prediction. Penguin UK.

Thorngate, W. & Edmonds, B. (2013) Measuring simulation-observation fit: An introduction to ordinal pattern analysis. Journal of Artificial Societies and Social Simulation, 16(2):14. http://jasss.soc.surrey.ac.uk/16/2/4.html

Watts, D. J. (2014). Common Sense and Sociological Explanations. American Journal of Sociology, 120(2), 313-351.

Edmonds, B., Polhill, G and Hales, D. (2019) Predicting Social Systems – a Challenge. Review of Artificial Societies and Social Simulation, 4th June 2019. https://rofasss.org/2018/11/04/predicting-social-systems-a-challenge


Some Philosophical Viewpoints on Social Simulation

By Bruce Edmonds

How one thinks about knowledge can have a significant impact on how one develops models as well as how one might judge a good model.

  • Pragmatism. Under this view a simulation is a tool for a particular purpose. Different purposes will imply different tests for a good model. What is useful for one purpose might well not be good for another – different kinds of models and modelling processes might be good for each purpose. A simulation whose purpose is to explore the theoretical implications of some assumptions might well be very different from one aiming to explain some observed data. An example of this approach is (Edmonds & al. 2019).
  • Social Constructivism. Here knowledge about social phenomena (including simulation models) are collectively constructed. There is no other kind of knowledge than this. Each simulation is a way of thinking about social reality and plays a part in constructing it so. What is a suitable construction may vary over time and between cultures etc. What a group of people construct is not necessarily limited to simulations that are related to empirical data. (Ahrweiler & Gilbert 2005) seem to take this view but this is more explicit in some of the participatory modelling work, where the aim is to construct a simulation that is acceptable to a group of people, e.g. (Etienne 2014).
  • Relativism. There are no bad models, only different ways of mediating between your thought and reality (Morgan 1999). If you work hard on developing your model, you do not get a better model, only a different one. This might be a consequence of holding to an Epistemological Constructivist position.
  • Descriptive Realism. A simulation is a picture of some aspect of reality (albeit at a much lower ‘resolution’ and imperfectly). If one obtains a faithful representation of some aspect of reality as a model, one can use it for many different purposes. Could imply very complicated models (depending on what one observes and decides is relevant), which might themselves be difficult to understand. I suspect that many people have this in mind as they develop models, but few explicitly take this approach. Maybe an example is (Fieldhouse et al. 2016).
  • Classic Positivism. Here, the empirical fit and the analytic understanding of the simulation is all that matters, nothing else. Models should be tested against data and discarded if inadequate (or they compete and one is currently ahead empirically). Also they should be simple enough that they can be thoroughly understood. There is no obligation to be descriptively realistic. Many physics approaches to social phenomena follow this path (e.g Helbing 2010, Galam 2012).

Of course, few authors make their philosophical position explicit – usually one has to infer it from their text and modelling style.


Ahrweiler, P. and Gilbert, N. (2005). Caffè Nero: the Evaluation of Social Simulation. Journal of Artificial Societies and Social Simulation 8(4):14. http://jasss.soc.surrey.ac.uk/8/4/14.html

Edmonds, B., le Page, C., Bithell, M., Chattoe-Brown, E., Grimm, V., Meyer, R., Montañola-Sales, C., Ormerod, P., Root H. and Squazzoni. F. (in press) Different Modelling Purposes. Journal of Artificial Societies and Social Simulation, 22(3):6. http://jasss.soc.surrey.ac.uk/22/3/6.html.

Etienne, M. (ed.) (2014) Companion Modelling: A Participatory Approach to Support Sustainable Development. Springer

Fieldhouse, E., Lessard-Phillips, L. and Edmonds, B. (2016) Cascade or echo chamber? A complex agent-based simulation of voter turnout. Party Politics. 22(2):241-256. DOI:10.1177/1354068815605671

Galam, S. (2012) Sociophysics: A Physicist’s modeling of psycho-political phenomena. Springer.

Helbing, D. (2010). Quantitative sociodynamics: stochastic methods and models of social interaction processes. Springer.

Morgan, M. S., Morrison, M., & Skinner, Q. (Eds.). (1999). Models as mediators: Perspectives on natural and social science (Vol. 52). Cambridge University Press.

Edmonds, B. (2019) Some Philosophical Viewpoints on Social Simulation. Review of Artificial Societies and Social Simulation, 2nd July 2019. https://rofasss.org/2019/07/02/phil-view/


A bad assumption: a simpler model is more general

By Bruce Edmonds

If one adds in some extra detail to a general model it can become more specific — that is it then only applies to those cases where that particular detail held. However the reverse is not true: simplifying a model will not make it more general – it is just you can imagine it would be more general.

To see why this is, consider an accurate linear equation, then eliminate the variable leaving just a constant. The equation is now simpler, but now will only be true at only one point (and only be approximately right in a small region around that point) – it is much less general than the original, because it is true for far fewer cases.

This is not very surprising – a claim that a model has general validity is a very strong claim – it is unlikely to be achieved by arm-chair reflection or by merely leaving out most of the observed processes.

Only under some special conditions does simplification result in greater generality:

  • When what is simplified away is essentially irrelevant to the outcomes of interest (e.g. when there is some averaging process over a lot of random deviations)
  • When what is simplified away happens to be constant for all the situations considered (e.g. gravity is always 9.8m/s^2 downwards)
  • When you loosen your criteria for being approximately right hugely as you simplify (e.g. mover from a requirement that results match some concrete data to using the model as a vague analogy for what is happening)

In other cases, where you compare like with like (i.e. you don’t move the goalposts such as in (3) above) then it only works if you happen to know what can be safely simplified away.

Why people think that simplification might lead to generality is somewhat of a mystery. Maybe they assume that the universe has to obey ultimately laws so that simplification is the right direction (but of course, even if this were true, we would not know which way to safely simplify). Maybe they are really thinking about the other direction, slowly becoming more accurate by making the model mirror the target more. Maybe this is just a justification for laziness, an excuse for avoiding messy complicated models. Maybe they just associate simple models with physics. Maybe they just hope their simple model is more general.


Aodha, L. and Edmonds, B. (2017) Some pitfalls to beware when applying models to issues of policy relevance. In Edmonds, B. & Meyer, R. (eds.) Simulating Social Complexity – a handbook, 2nd edition. Springer, 801-822.

Edmonds, B. (2007) Simplicity is Not Truth-Indicative. In Gershenson, C.et al. (2007) Philosophy and Complexity. World Scientific, 65-80.

Edmonds, B. (2017) Different Modelling Purposes. In Edmonds, B. & Meyer, R. (eds.) Simulating Social Complexity – a handbook, 2nd edition. Springer, 39-58.

Edmonds, B. and Moss, S. (2005) From KISS to KIDS – an ‘anti-simplistic’ modelling approach. In P. Davidsson et al. (Eds.): Multi Agent Based Simulation 2004. Springer, Lecture Notes in Artificial Intelligence, 3415:130–144.

Edmonds, B. (2018) A bad assumption: a simpler model is more general. Review of Artificial Societies and Social Simulation, 28th August 2018. https://rofasss.org/2018/08/28/be-2/


The “Formalist Fallacy”

By Bruce Edmonds

This is the tendency to believe theories more if they are formalised (e.g. as sets of mathematical equations or computer simulations).

This can be simply an effect of Kuhn’s “Theoretical Spectacles” (1962) — due to the fact we can clearly see how a complex mechanism might result in some particular outcomes (due to the formal model) then we project this onto the world. That is, we fit our perception of some part of the world into the conception illustrated by the model. This is the opposite way to how science is supposed to work, where the model should be adjusted (or rejected) in light of the evidence.

Another reason for more readily accepting theories expressed in terms of mathematics is that maths has status. It used to be the case that mathematical models were the only practical formal technique, which is why science became associated with maths. Thus you are much more likely to be published in many journals if your paper is expressed mathematically, regardless of whether the formalism is used to prove or calculate anything.

If an idea is expressed in informal ways then we are freer to express doubt, as we have an instinctual idea of how slippery natural language statements can be. We know that humans are lazy and thus have a tendency to believe their own ideas, unless pretty well forced to change (e.g. by evidence). It should be the case that making ideas precise makes them easier to disprove (as in Popper 1963) but this is only the case if the mapping between the model and what it refers to is also precise. Otherwise one is free to imagine how a model could apply, giving the illusion of generality.

For example, Eckhart Arnold (2005) shows, in detail, how game theoretical models based on around the ‘Prisoner’s Dilemma’ (e.g. Axelrod 1984) fail to have empirical relevance. Other abstract models that have had many citations but do not seem to connect well to evidence include: (Schelling 1971), Hegselmann & Krause (2002) and Deffaunt et al (2002). Each of these is simple, formal but has interesting outcomes. As a result they seem apparently irresistible to other researchers with many citations and influence but no direct modelling relation with the observed world. This contrasts with modelling papers which compare simulated and real-world data (Chattoe-Brown 2018).

Do not mistake me – I think formalising ideas is very useful. It makes sharing the ideas without error or reinterpretation possible, allowing a community of researchers to critique, improve, check, and apply them (Edmonds 2000). It should also be easier to check if they actually work – for example if they do predict some unknown and measurable aspects of an observed system. It is just that formalism, of itself, does not make them more likely to be true (or the resulting models useful for anything that reliably relates to the observed world) but we are more likely to think they are, due to our tendency to project what we clearly understand.


Arnold, E. (2008). Explaining altruism: A simulation-based approach and its limits (Vol. 11). PhD Thesis. Walter de Gruyter. http://www.phil-fak.uni-duesseldorf.de/fileadmin/Redaktion/Institute/Philosophie/Theoretische_Philosophie/Allgemein/Hilfskraefte/Explaining_Altruism-colored_figures.pdf

Axelrod, Robert. 1984. The Evolution of Cooperation. Basic Books.

Chattoe-Brown, E. (2018) What is the earliest example of a social science simulation (that is nonetheless arguably an ABM) and shows real and simulated data in the same figure or table? Review of Artificial Societies and Social Simulation, 11th June 2018. https://roasss.wordpress.com/2018/06/11/ecb/

Deffuant, G., Amblard, F., Weisbuch, G. and Faure, T. (2002) How can extremism prevail? A study based on the relative agreement interaction model. Journal of Artificial Societies and Social Simulation 5(4), 1. http://jasss.soc.surrey.ac.uk/5/4/1.html

Edmonds, B. (2000) The Purpose and Place of Formal Systems in the Development of Science, CPM Report 00-75, MMU, UK. http://cfpm.org/cpmrep75.html

Hegselmann, R. and Krause, U. (2002). Opinion Dynamics and Bounded Confidence Models, Analysis and Simulation. Journal of Artificial Societies and Social Simulation, 5(3), 2. http://jasss.soc.surrey.ac.uk/5/3/2.html

Kuhn, T.S. (1962) The Structure of Scientific Revolutions. University of Chicago Press.

Popper, K. (1963). Conjectures and refutations: the growth of scientific knowledge. London: Routledge.

Schelling, T. C. (1971). Dynamic models of segregation. Journal of mathematical sociology, 1(2), 143-186.

Edmonds, B. (2018) The "formalist fallacy". Review of Artificial Societies and Social Simulation, 11th June 2018. https://rofasss.org/2018/07/20/be/