What's wrong with social simulations?

Eckhart Arnold

1 Introduction
2 Simulation without validation in agent-based models
3 How a model works that works: Schelling’s neighborhood segregation model
4 How models fail: The Reiterated Prisoner’s Dilemma model
5 An ideology of modeling
6 Conclusions

4 How models fail: The Reiterated Prisoner’s Dilemma model

Robert Axelrod’s computer simulations of the Reiterated Prisoner’s Dilemma (RPD) (Axelrod 1984) are well known and still considered by some as a role model for successful simulation research (Rendell et al. 2010a, 408-409). What is not so widely known is that the simulation research tradition initiated by Axelrod has remained entirely unsuccessful in terms of generating explanations for empirical instances of cooperation. What are the reasons for this lack of explanatory success? And how come that Axelrod’s research design is none the less considered as a role model today?

Axelrod had the ingenious idea to advertise a public computer tournament where participation was open to everybody. Participants were asked to hand in their guess at a best strategy in the reiterated two person Prisoner’s Dilemma in the form of an algorithmic description or computer program. This provided Axelrod with a rich, though naturally very contingent set of diverse strategies and it had the, surely welcome, side-effect of generating attention for Axelrod’s research project. Axelrod ran a sequence of two tournaments. As is well known the rather simplistic strategy Tit For Tat won both tournaments.

In the Prisoner’s Dilemma Game the players can decide whether to cooperate or not to cooperate. Mutual cooperation yields a higher payoff than mutual non-cooperation, but it is best to cheat by letting the other player cooperate while not cooperating oneself. And it is worst to be cheated, i.e. to cooperate while the other player does not. Tit For Tat cooperates in the first round of the Repeated Prisoner’s Dilemma, but if the other player cheats, then Tit For Tat will punish the other player by not cooperating in the following round.[8] Axelrod analyzed the course of the tournament in order to understand just why Tit For Tat was such a successful strategy. He concluded that it is a number of characteristics that determine the success of a strategy in the Reiterated Prisoner’s Dilemma (Axelrod 1984, chapter 6): Successful strategies are (1) “friendly”, i.e. they start with cooperative moves, (2) envy-free, (3) punishing, but also (4) forgiving. Axelrod furthermore believed that repeated interaction is a necessary requirement for cooperation to evolve and that, of course, Tit For Tat is generally quite a good strategy in Reiterated Prisoner’s Dilemma situations.

Unfortunately for Axelrod, the Reiterated Prisoner’s Dilemma model is anything but robust. For each of his conclusions, variations of the RPD-model can be constructed where the conclusion becomes invalid (Arnold 2013, 107). It is even possible to construct a variant that allows strategies to break off the repeated interaction at will and that does not lead to the breakdown of cooperation (Schuessler 1990). The failure to derive any robust results highlights the danger of drawing generalizing conclusions from models and of relying on models as a tool of theoretical investigation. This point has most strongly been emphasized by Ken Binmore, who describes the popularity that Axelrod’s model enjoyed derogatorily as the “The Tit-For-Tat Bubble” (Binmore 1994, 194). Because the folk theorem from game theory implies that there are infinitely many equilibria in the Reiterated Prisoner’s Dilemma, there is not much reason to assign of all things the Tit For Tat-equilibrium a special place (Binmore 1994, 313-317). If one follows Binmore’s criticism then it is not the reiterated Prisoner’s Dilemma that explains why Tit For Tat is such a good strategy, but rather the fact that Tit For Tat is a very salient and easily understood mode of behavior in many areas of life that explains why people so easily believed in the superiority of the Tit For Tat strategy in the RPD game.

It is not only its lack of robustness that troubles Axelrod’s model. It is also the difficulty of relating it to any concrete empirical subject matter – a problem that Axelrod shares with many game theoretical explanations.[9] Axelrod himself had offered a very impressive example of empirical application by relating the RPD model to the silent “Live and Let Live” agreement that emerged between enemy soldiers on some of the quieter stretches of the western front in the First World War. However, as critics were quick to point out (Battermann et al. 1998, Schuessler 1990), it is not at all clear whether this situation really is a Prisoner’s Dilemma situation, let alone how the numerical values of the payoff parameters could be assessed. But precise numerical payoff values would be necessary since Axelrod’s model is not robust against changes of the numerical values of the payoff parameters within the boundaries that the Prisoner’s Dilemma game allows (Arnold 2008, 80). Also, Axelrod’s model could not explain why “Live and Let Live” occurred only on some stretches of the front line (Arnold 2008, 180). Therefore, Axelrod’s theory of the evolution of cooperation could not really add anything substantial to the historical explanation of the “Live and Let Live” by Tony Ashworth (1980).

The chapter from Axelrod’s book on the “Live and Let Live”-system shows that he did not understand his model only as a normative model, but at least also as an explanatory model. And the model was certainly understood as potentially explanatory by the biologists who were trying to apply it to cooperative behavior among animals (see below). The distinction is important, because the validation requirements for normative models are somewhat relaxed in comparison to explanatory models. After all, we would not expect from a model that is meant to generate advice for rationally adequate behavior to correctly predict the behavior of unadvised and potentially irrational agents. Still, even normative models must capture the essentials of the empirical situations to which they are meant to be applied well enough to generate credible advice. Here, too, robustness is an important issue. For similar reasons as in the descriptive case it would be dangerous to trust the advice given on the basis of a non-robust model.

Thus, in contrast to Schelling’s model Axelrod’s model is neither robust nor can the postulated driving factors of the emergent phenomenon (stable cooperation) easily be identified empirically. In Schelling’s case the driving factor was the assumed tolerance threshold, in Axelrod’s case it is the payoff parameters of the Prisoner’s Dilemma. Therefore, two important prerequisites (robustness and empirical identifiability) for the application of a formal model to a social process appear to be absent in Axelrod’s case.

The popularity of Axelrod’s computer tournaments had the consequence that it became a role model for much of the subsequent simulation research on the evolution of cooperation. It spawned myriads of similar simulation studies on the evolution of cooperation (Dugatkin 1997, Hoffmann 2000). Unfortunately, most of these simulation studies remained unconnected to empirical research. Axelrod had – most probably without intending it – initiated a self-sustaining modeling tradition where modelers would orientate their next research project on the models that they or others had published before without paying much attention to what kind of models might be useful from an empirical perspective. Instead it was more or less silently assumed that because of the generality of the model investigations of the reiterated Prisoner’s Dilemma model would surely be useful.

How little contact the modeling tradition initiated by Axelrod had to empirical research becomes very obvious in a survey of empirical research on the evolution of cooperation in biology by Dugatkin (1997). In the beginning, Dugatkin lists several dozens of game theoretical simulation models of the evolution of cooperation, an approach to which Dugatkin himself is very favorable. However, none of the models can be related to particular instances of cooperation in animal wildlife. A seemingly insurmountable obstacle in this respect is that payoff parameters usually cannot be measured. It is just very difficult to measure precisely the increased reproductive success, say, that apes that reciprocate grooming enjoy over apes that don’t.

The most serious attempt to apply Axelrod’s model was undertaken by Milinski (1987) in a study on predator inspection behavior in shoal fishes like sticklebacks. When a predator approaches, it happens that one or two sticklebacks leave the shoal and carefully swim closer to the predator. The hypothesis was that if two sticklebacks approach the predator they play a Reiterated Prisoner’s Dilemma and make the decision to turn back based on a Tit For Tat strategy taking into account whether the partner fish stays back or not. This was tested experimentally by Milinski (1987) as well as others (Dugatkin 1998, 59-69). While in his 1987-paper Milinski himself believed that the hypothesis could be confirmed, it was after a long controversy ultimately abandoned. In a joint paper on the same topic that appeared ten years later Milinski/Parker (1997) do not draw on the RPD model any more. In fact they treat it as an unresolved question whether the observed behavior is cooperative at all.

In a later discussion, Dugatkin explained the problem when linking the model research about cooperation to the empirical research in biology by the difficulty of establishing a feedback-loop between model research and empirical research (Dugatkin 1998a, 57-58). The empirical results were never fed back into the model building process and the obstacles when trying to apply the models were never considered by the modelers. Without a feedback-loop between theoretical and empirical research, however, the model-building process soon reaches a stalemate where models remain detached from reality.

The frustration about this kind of pure model research is well expressed in a polemical article by Peter Hammerstein (2003). “Why is there such a discrepancy between theory and facts?” asks Hammerstein (2003, 83) and continues: “A look at the best known examples of reciprocity shows that simple models of repeated games do not properly reflect the natural circumstances under which evolution takes place. Most repeated animal interactions do not even correspond to repeated games.” In saying so, Hammerstein is by no means opposed to employing game theory in biology. It’s just that in the aftermath of Axelrod most simulation studies on the evolution of cooperation focused on the Reiterated Prisoner’s Dilemma or similar repeated games. This shows that the demand for empirical validation has an important side effect besides allowing to judge the truth and falsehood of the models themselves: It forces the modelers to concern themselves seriously with the empirical literature and the empirical phenomena that their models address. If they do so, there is hope that this will lead quite naturally to the choice of simulation models that address relevant questions of empirical research. Or, as Hammerstein (2003, 92) nicely puts it: “Most certainly, if we invested the same amount of energy in the resolution of all problems raised in this discourse, as we do in the publishing of toy models with limited applicability, we would be further along in our understanding of cooperation.”

Just how little model researchers care for the empirical content of their research is inadvertently demonstrated by a research report on the evolution of cooperation that appeared roughly 20 years after the publication of Axelrod’s first paper about his computer tournament (Hoffmann 2000). There is only one brief passage where the author of this research report talks about empirical applications of the theory of the evolution of cooperation. And in this passage there is but one piece of empirical literature that the author quotes, the study on predator inspection in sticklebacks by Milinski (1987)! Nevertheless, Hoffmann believes that the “general framework is applicable to a host of realistic scenarios both in the social and natural worlds” (Hoffmann 2000, 4.3). Much more believable is Dugatkin’s summary of the situation: “Despite the fact that game theory has a long standing tradition in the social sciences, and was incorporated in behavioral ecology 20 years ago, controlled tests of game theory models of cooperation are still relatively rare. It might be argued that this is not the fault of the empiricists, but rather due to the fact that much of the theory developed is unconnected to natural systems and thus may be mathematically intriguing but biologically meaningless” (Dugatkin 1998a, 57). That this fact could escape the attention of the modelers tells a lot about the prevailing attitude of modelers towards empirical research.

[8] For a detailed description RPD-model and the tournament see Axelrod (1984). An open-source implementation is available from: www.eckhartarnold.de/apppages/coopsim.

[9] This is very frankly admitted by the leading game theorist Rubinstein (2013) in a newspaper article. Rubinstein resorts to an aesthetic vindication of game theory (“flowers in the garden of God”).

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