Note: This is an edited version of the paper I gave at the 2016 SAA session organized by Ben Davies.

Simulation can be used to do anything. That’s part of its problem. It can easily be used try to replicate a particular past context. But should it? Anyone who has tried to build general archaeological models has been asked by a colleague: Can this thing model my valley? The simple answer is that it can. I will argue that it shouldn’t. Instead, we should ask our colleagues whether they recognize their valley in some regions of the output of our simulations.

To put it in terms of the title of the SAA session for which I wrote this paper, should archaeological simulation aim at modeling past people, places and things, or should it aim at modeling particular past people, particular places and particular things? I will argue that it is more helpful to model pasts, plural, than it is to model any particular past. I will argue that trying to model specific sequences of events, carried out by specific people, in specific places, with specific things, is less useful than modeling general systems that generate patterns of evidence in which we recognize, or sometimes more importantly in which we don’t recognize the particular people, places and things of the past in which we are interested.

What do we know?

When we build models of certain specific people, places and things, we ignore an unknown number of unknown factors of unknown magnitude and significance. In the modeling process, we inevitably and consciously select potentially significant variables, from topography and climate, to post-marital residence patterns, to the mechanical properties of raw materials, to the nutritional value of anatomical elements, among a multitude of others.

We know very well what we put into a model, or at least we ought to. But we only know some of what we don’t include. We have no idea of most of what we don’t include and how that might shape the output.

By giving our factors specific values that we expect will map onto a particular imagined past, we further cut ourselves off from a multitude of possible pasts, an unknown number of which could equally, or better, have produced our observed or target evidence.

There is an echo here of the tyranny of the ethnographic record, in which Martin Wobst (1978) argues on the one hand that we shouldn’t ignore the past human behaviour to which we don’t have access, and on the other, that we shouldn’t feel constrained by the present human behaviour to which we happen to have access in the present. There is also the haunting specter of Edmund Leach’s (1973) powerful and intuitive condemnation of archaeology in general, and particularly of archaeological modeling, as the art of the black box.

Let’s consider what is often thought of as the relatively simple matter of topography, and the well-specified question of transport cost: while we can certainly figure out some of the features of a landscape that would have been significant to a population in terms of transport cost, such as slope, ground cover, and a few other standards, we simply have no way of knowing, a priori, which other features of a landscape were significant to a particular group of people, at a particular place and time, what their relative significances were, or how and to what extent, transport cost affected people’s decisions and behaviours. Place avoidance, memory, beliefs, are all factors which are not typically included in our cost surfaces. Not all optimization targets are physical, and not all behaviours are optimizing. In a sense, any human problem is an infinite problem.

What can we do?

Despite their infinity, I do believe we can usefully study human problems and that simulation is a useful tool for us. In the case of transport cost, for example, we can learn at the very least about which features are not likely to have been important, and we can learn whether the usual suspects that generate the physical friction in our models are completely insufficient to account for a particular transport pattern. But we can only take the next step and find out what kinds of other factors might explain the discrepancy, by creating a very large universe of transport cost structures, and letting our simulations wander through it. No amount of specifying will help us move beyond the intuitive ruling out of factors, one by one. Thanks to faster and more available computing power, this forever wandering through an infinite universe of possibilities, looking for familiar features and configurations, is not as impractical as it used to be, but I doubt it will ever be sufficient, no matter how fast and powerful our tools get.

For this searching for familiar places through constellations of transport cost configurations to be helpful, even in theory, we must do radical things, like letting go of our map fetish, for instance. Many of us have an irrational, emotional attachment to maps and DEMs. Applying our vast universe of transport cost structures to an in silico representation of a specific, real-world topography, even the very carefully, latest LIDARed, most pollen profiled, downscaled precipitation, general circulation modeled, paleo-environment, will only let our simulation explore one abstraction of one of the possible worlds that could have produced our observed evidence. In fact, the more we throw into our map, the more accurate we try to make it, the more worlds we ignore, and the more abstraction we produce. And we’re not done. We must still apply our universe of cost structures to a universe of possible environments, and let our simulation wander through that.

The reason is that our very carefully reconstructed and specified environment suffers from the same defects as any specific model. It ignores an unknown number of unknown features of unknown magnitude and significance.

Only when we’ve produced a universe of possibilities, can we look at the resulting parameter space and look for our valley. We may find it in many places. Or at least, we may find many places in that space, many sectors, that remind us of our valley in various ways. Perhaps a more important result is that in large sectors of that space, we won’t find anything that looks remotely like our valley. By finding our valley in several (or hopefully many) regions of our landscape, we can start to ask ourselves how to determine which ones are more likely to actually be like our valley.

What can we learn?

Finding these regions that are morphologically similar to our target past, our proverbial valley, can be helpful and can help inform further simulation experiments.  The morphology is one thing, but the formation processes, the mechanisms, those are the real target. Two places that are equally reminiscent of our valley can be the result of the operation of radically different sets of processes. This is certainly less challenging than the alternative, but much more interesting case, in which our valley and a region that looks radically different are in fact generated by the same set of processes. Here is the true black box, and one of the main problems of simulation as an approach.

In contrast to that weakness, the fundamental strength of simulation as an approach to the study of the past is not that it allows us to reproduce archaeologically observed data, but that it allows us to posit mechanisms, and to watch them operate, and to watch them produce observable outcomes. Instead of looking at simulation results for accurate portraits of past contexts, or rather as reflections of past contexts that produced a set of archaeological evidence observable in the present, we should search past contexts for evidence of the operation of mechanisms that we have seen unfold in simulation.

As archaeological simulators, Demiurges, as Colin Renfrew (1982) would have it, we have to wean ourselves from realism. We make a serious error when we imagine that a careful reconstruction of a real-world environment is any less imaginary than one that is explicitly hypothetical and imaginary. In fact, a set of imaginary landscapes, collectively, are far more useful, and in some ways, far more real than any single realistic counterpart, no matter how carefully specified and documented. This holds true for any part of a past human system in which we are interested, and is the only way to seriously tackle Leach’s challenge.

I am very consciously making the argument that the positing of mechanisms and the watching of unfolding simulation outcomes (the original evolutio, or unfolding) is prior to, and in many ways independent from, the understanding of specific archaeological contexts.

We shouldn’t search for mechanisms that can produce our archaeological contexts. We should search for archaeological contexts that can be produced by our mechanisms.

After all, Demiurges create worlds. They don’t try to make copies of worlds. As simulators, we should be confident in our creative power and its usefulness.  We should create worlds and let archaeological contexts replicate them.

Next time a colleague eagerly asks you “can you model my valley?”, show them some simulation output and ask them – “do you see your valley in here anywhere?”


Leach E 1973. Concluding address, in C Renfrew (ed) The explanation of culture change: models in prehistory. Duckworth, London :761-771.


Renfrew C 1981. The simulator as demiurge, in JA Sabloff (ed) Simulations in archaeology, University of New Mexico Press, Albuquerque :283-306.


Wobst HM 1978. The Archaeo-Ethnology of Hunter-Gatherers or the Tyranny of the Ethnographic Record in Archaeology, American Antiquity 43:303-309.

2 thoughts on “Can you model my valley? Particular people, places and times in archaeological simulation

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