, Volume 70, Issue 1, pp 3–27 | Cite as

Credible Worlds, Capacities and Mechanisms

Original Paper


This paper asks how, in science in general and in economics in particular, theoretical models aid the understanding of real-world phenomena. Using specific models in economics and biology as test cases, it considers three alternative answers: that models are tools for isolating the ‘capacities’ of causal factors in the real world; that modelling is ‘conceptual exploration’ which ultimately contributes to the development of genuinely explanatory theories; and that models are credible counterfactual worlds from which inductive inferences can be made. The paper argues that the ‘credible worlds’ account captures significant aspects of scientific practice, even if many modellers see their work as conceptual exploration.

1 Introduction

Economic theorists construct highly abstract models. If interpreted as representations of the real world, these models appear absurdly unrealistic; yet economists claim to find them useful in understanding real economic phenomena. This prompts the question: Do these models really help us to understand the world, and if so, how?

This is a question not only for philosophers of science but also for practising economic theorists such as myself. Trying to sort out my ideas some years ago, I wrote a paper, ‘Credible worlds’ (Sugden 2000). Using two famous modelling exercises as examples—George Akerlof’s (1970) model of the used car market and Thomas Schelling’s (1978) model of racial segregation—I looked at what those modellers actually said about the relationship between model and world. Each paper contains frequent references to real-world phenomena; these references make sense only on the supposition that the models are intended to explain those phenomena. But each author is remarkably inventive in finding ways of suggesting that his model tells us about the world while avoiding any concrete claims about what it does tell us. I tried to find an explanation of what these modellers were doing that was consistent with this puzzling imprecision. I offered an account of models as credible but counterfactual worlds, paralleling the real world rather than isolating features of reality. I argued that the gap between model world and real world has to be crossed by inductive inference, and that inductive inference depends on subjective judgements of ‘similarity’, ‘salience’ and ‘credibility’ which cannot be formulated in the mathematical and logical languages preferred by economic theorists. Imprecision of language when moving from one world to the other serves to hide embarrassment about claiming validity for inductive inferences. The present paper offers some further reflections on the ‘credible worlds’ argument, and responds to various criticisms of that argument, particularly by other authors in the present symposium and by Emrah Aydinonat (2007).

Some readers may be inclined to think that the imprecision with which we economists speak about how our theoretical models relate to the world is a sign of the weakness of our claim to be scientists. Indeed, Nancy Cartwright (2009) has contrasted the work of economists and physicists, arguing that models in economics differ from those of physics in failing to provide an adequate basis for induction to the real world. So it is relevant to ask whether natural scientists are less reticent about what can be learned from abstract models, and about how it is learned. I will argue that the puzzling features of economists’ discussions of their models are paralleled in some of the work of theoretical biologists.

In the decade since I first presented the ‘credible worlds’ argument, I have discussed my ideas with many methodologists of economics, and I have had many more opportunities to study what economic modellers do. In my discussions with methodologists, I have found that two contrasting accounts of the role of theoretical models in economics are particularly widely held. The first is that models are tools for isolating ‘tendencies’ or ‘capacities’ that operate in the real world but which, because of the complexity of real environments, are difficult to investigate directly. The second account is that models do not tell us anything about the real world; they merely provide abstract components which may prove useful in developing genuinely explanatory theories. In this symposium, most of the criticisms of the credible worlds argument are made from one or other of these two standpoints. As a participant observer of the practices of economics, my sense is that most theoretical modellers are inclined towards the second account: they feel most comfortable when describing their work in these terms. However, I still believe that the credible worlds account captures significant features of how models are used in economics.

In this paper, I contrast the ‘credible worlds’ conception of modelling with each of its main rivals. The idea that models are isolating tools will be represented by the work of Nancy Cartwright. In presenting the idea that models do not tell us about the world, I draw on Thomas Schelling’s discussion of ‘social mechanisms’.

It will help to avoid confusion if I say straight away that, in this paper, I am not directly concerned with questions about the nature of scientific knowledge—for example, about whether claims to economic knowledge should be understood in terms of the conceptual schemes of realism, instrumentalism or pragmatism.1 My concern is with a question that is closer to the consciousness of most practising economists—how, or whether, theoretical models help us to understand the world, whatever philosophical gloss is given to the concept of ‘understanding’.

2 A Sketch of the Terrain

This paper is about theoretical models, primarily in economics. Since I will not be concerned with other types of model, I will from now on drop the qualifier ‘theoretical’.

It is surely uncontroversial that in most economic models, the entities that are assembled and manipulated are labelled in ways that refer to real-world correlates. Sometimes this labelling uses ordinary, non-technical language (for example, models may contain ‘individuals’ with ‘preferences’ over ‘goods’, or ‘firms’ which seek ‘profit’). In other cases, technical economic terms are used (for example, ‘utility’, ‘subjective probability’ or ‘signal’); but these terms often have reasonably straightforward translations into ordinary language. When the entities of the model are interpreted according to these labels, their interactions in the model normally make at least rough intuitive sense, a sense that modellers sometimes acknowledge by speaking about the ‘story’ embedded in a model. A related metaphor is implicit in the familiar idea of the ‘real world’. The opposite of the real world is the model world—the world that the model describes. The point of all this is that the properties of the model, and the manipulation of these properties by the modeller, can be described in two parallel ways. They can be described in formal, abstract terms, with no significance being attached to the ordinary-language meaning of the labelling; or they can be described as propositions about an imaginary but imaginable world.

Consider a model that is fully specified by the set of properties A = {A1,…, An}. Suppose that if we take the corresponding formal propositions and apply accepted principles of mathematics and deductive logic, we derive a proposition that corresponds to the property R. One standard way of describing what we have done is to say that A1,…, An are the assumptions of the model, and R is a result. We might also say that we have investigated a model world with properties A1,…, An, and have shown that it also has (indeed, must have) property R. Or, we might say that we have shown that ifA1,…, An were properties of the real world, thenR would (necessarily) be a property of the real world too. In many modelling exercises, it makes sense to describe the relationship between A1,…, An and R as a mechanism by which A1,…, An interact to bring about R. Then we can say that this mechanism operates in the model world, and that if A1,…, An were properties of the real world, then it would operate in the real world too.

One option is simply to stop at this point. This gives us an understanding of modelling according to which models do not tell us anything substantive about the real world; they are merely tools for what Daniel Hausman (1992, p. 221) calls “conceptual exploration”.

A second option corresponds with my understanding of the idea that models are isolating tools. Suppose that A can be partitioned into three subsets, L = {L1,…, L}, S = {S1,…, Ss} and X = {X1,…, Xx}. L1,…, L are interpreted as empirical laws whose truth is beyond reasonable doubt: we can say that we know that L1,…, L are properties of the real world. S1,…, Ss are interpreted as substantive assumptions, while X1,…, Xx are auxiliary assumptions. (I will explain what I mean by this distinction in the next paragraph; until then, nothing hangs on it.) We can now re-describe the modelling exercise by omitting explicit reference to the laws. We can say that we have investigated a model world with properties S1,…, Ss, X1,…, Xx, and have shown that it also has property R. (In saying this, we taking it as read that any model world should satisfy what Mäki (2009) calls the ‘way the world works’ constraint.) Or we can say that we have shown that ifS1,…, Ss, X1,…, Xx were properties of the real world, thenR would be a property of the real world too. We can treat the relationship between S1,…, Ss, X1,…, Xx and R as the mechanism exhibited by the model. This mechanism operates in the model world. If S1,…, Ss, X1,…, Xx were properties of the real world, it would operate in that world too. Notice that, if we follow this strategy, we generate empirical ifthen…propositions rather than necessary truths. Because these propositions have been reached by deductive reasoning, using as premises only known empirical laws, they are firmly grounded. It seems that we are entitled to say that we know they are true.

This approach can be refined by using the distinction between substantive and auxiliary assumptions. Suppose that, for whatever reason, we think of the substantive assumptions as essential components of the mechanism we are describing, and the auxiliary assumptions as merely providing a medium in which that mechanism can work. We investigate many models, all of which use the same S (and L) assumptions as before, but with different specifications of X. We find that, in all these models, R can be derived as a result. One way of describing this exercise is as a robustness test: we have found that the link between S and R is robust. Then, we might make the inductive inference that, in any model with these S (and L) properties, it is very probably the case that R can be derived. An equivalent inference is that, ifS1,…, Ss were properties of the real world, then (very probably) R would be too. This ifthen…proposition specifies what Cartwright would call a capacity.

On this understanding, there is a significant analogy between models and experiments. In setting up a model with L, S and X as the assumptions, we are asking what would happen if we created a real-world situation with properties S and X. We could carry out this investigation experimentally by setting up such a situation and waiting to see the effects of whatever empirical laws really are in operation. In using the model instead, we assume that we already know the relevant laws (these are contained in L), and simulate their operation. Similarly, robustness tests in modelling simulate robustness tests in experimentation. A capacity can be demonstrated either by a robust modelling result or by a robust experimental finding.

The isolation approach allows us to understand modelling as a source of firmly-grounded substantive knowledge about the real world. But there is snag: in the context of typical modelling exercises in economics, this approach generates very little knowledge. Economic models typically contain many substantive assumptions, which do most of the work in generating the results. Known empirical laws contribute rather little.

If that is right, there seem to be at least three alternative responses for economists to take. The first is to acknowledge that models do not tell us anything substantive about the real world, but still to defend modelling as a useful activity. That leaves us with conceptual exploration. The second is to insist that modelling is useful only in so far as it generates firmly-grounded knowledge about capacities, and to conclude that the value of modelling in economics is rather low. That, roughly, is Cartwright’s response. The third is to look for something less than firmly-grounded knowledge, and to argue that modelling can support beliefs or conjectures about substantive properties of the real world. That is what the credible worlds account of modelling tries to do.

I contend that, in their practice, economic theorists are unwilling to take either of the first two approaches wholeheartedly. Intuitively, they believe that their models support conjectures about the real world, and they want to communicate those conjectures in a convincing way. But the conjectures they want to make cannot be supported by deductive argument, even if that is supplemented by the circumscribed form of inductive inference that supports conclusions about robustness. They ease this tension by avoiding explicit claims about how their models relate to the real world, leaving their readers to make the necessary inferences themselves.

To clarify this contention, consider again the case of a model which is fully specified by some set of empirical laws L, some set of substantive assumptions S, and some set of auxiliary assumptions X. Suppose the result R is derived, and that this finding is robust to changes in the specification of X. Suppose too that we know that the real world has property R, but not whether it has the properties S1,…, Ss. Does the model support the conjecture that S1,…, Ss are properties of the real world? Putting this another way, in our family of model worlds, there is a common mechanism which reliably generates a property that we observe in the real world. Does this support the conjecture that a similar mechanism is operating in the real world? If we confine ourselves to deductive reasoning and robustness analysis, the answer to these questions is surely “No”. But modellers often seem to want to claim that conjectures of this kind are supported by their models, even if they stop just short of making these claims explicit. Implicitly, they seem to be using some kind of abductive inference (inferring causes from effects).2 The credible worlds account is an attempt to understand how models can support conjectures about the real world.

3 An Example from Economics: Banerjee’s Herding Model

Since I am concerned with what modellers actually do, it is important to work with concrete examples. I will not rehearse my previous analysis of Akerlof’s and Schelling’s models, but take that as read. To avoid repetition, I use a new example from economics: the much-cited paper in which Abhijit Banerjee (1992) presents a model of “herding behaviour”.

Banerjee’s opening paragraph skims over a range of social and economic situations in which there is a tendency for herding or clustering—for people to choose particular options because other people are choosing them. Some of Banerjee’s examples—people patronising particular shops, restaurants or schools just because they are popular, academics choosing particular research topics just because other academics are doing so—are drawn from what he takes to be the common experience of his readers. Others—herding behaviour in decisions about financial assets, about whether to have children, and about voting—have been reported in the literature of social science. Banerjee then declares his objective: “The aim of this paper is to develop a simple model in which we can study the rationale behind this kind of decision making as well as its implications” (p. 798). Notice that the model is intended as an investigation of the rationale—by which I take Banerjee to mean a rational-choice explanation—of a type of behaviour whose existence in the real world is taken as a fact.

Banerjee begins his analysis with a stripped-down version of his model. Two restaurants, A and B, are located next to one another. There are 100 consumers, each of whom wants to eat at the better restaurant. One restaurant is in fact better than the other, but no one is sure which is better and which is worse. There is a prior probability of 0.51 that A is better; this is common knowledge among consumers. In addition, each consumer receives a private and independent signal which indicates with high (but not perfect) reliability which really is better. Consumers arrive at the restaurants in sequence. On arrival, each consumer can see how many previous arrivals have gone to each restaurant. Suppose that one consumer receives a signal indicating that A is better, and that he is the first arrival; all the others receive signals favouring B. It is rational for the first arrival to choose A. But then the second arrival can infer that the first arrival’s signal favoured A. Since the prior probability that A is better is greater than 0.5, the posterior probability that A is better, conditional on one signal favouring A and one favouring B, is greater than 0.5 too; so it is optimal for the second arrival to go to A. The third arrival sees that the first and second have chosen A. That the first arrival has chosen A is evidence that his signal favoured A. That the second arrival, knowing this, chose A provides no additional information (since she would have chosen A whatever her own signal). But still, this is enough information to make A the best choice for the third arrival, even though his signal favours B. And so it continues: everyone ends up at A, even though their aggregate information makes it virtually certain that B is better.

Most of the rest of the paper is devoted to the analysis of a more sophisticated variant of the restaurant model. Banerjee derives a number of striking results about Bayesian-Nash equilibrium in this model. The main result is that, with very high probability, the equilibrium outcome is inefficient. (As in the restaurant case, everyone clusters at the option chosen by the first arrival.) A subsidiary result is that the equilibrium outcome is highly volatile across different plays of the game.

Towards the end of the paper, Banerjee discusses possible “extensions and modifications” of the basic model. These respond to potential criticisms of the realism of his assumptions as representations of real-world environments. In some cases, he concedes that his assumptions are unrealistic, but shows that his results are robust to more realistic re-specifications of the model. For example, reviewing the assumption that all individuals who choose the same option receive the same payoff, he says that this may be approximately correct in the restaurant case, but in “many other real world examples” payoffs may depend on who chose which option first. He shows that his main qualitative results still hold if payoffs have this property. In other cases, he appeals to facts about the real world to support the claim that, despite appearances to the contrary, the assumptions are adequately realistic. For example, he considers the criticism that the model should take account of incentive mechanisms that might be put in place to counteract herding. His response is that “in many of the cases we consider” effective incentive systems are infeasible.

These “extensions and modifications” reconfirm that Banerjee’s objective is to explain real-world phenomena. Notice that realism is defined relative to a set of “cases we consider”: the implication is that there is some set of real-world phenomena, specified independently of the model, which the model is to explain. But what inferences about these phenomena should we draw? On this, Banerjee is almost completely silent.

Apart from the passages I have already quoted, I can find only two sentences which refer to inferences from the model to the real world. The first comes after the presentation of the result that, in the model, equilibrium is volatile. Banerjee says: “This may shed some light on observations of ‘excess volatility’ made in the context of many asset markets and the frequent and apparently unpredictable changes in fashions” (p. 800). Here, there is a claim that the model tells us (or, at least, may tell us) something about the real word; but the wording seems deliberately vague about what we are told. The second sentence follows a discussion of a rival explanation of herding, which assumes that the agents who herd are rewarded for convincing third parties that their decisions are correct. Banerjee notes that this assumption does not apply to many of the cases he is considering, and concludes: “It is therefore useful to establish that inefficient herd behavior can arise even when the individuals themselves capture the rewards from their decisions” (p. 801). Here, I take it, Banerjee is claiming that his model is better able than its rival to explain some significant real-world instances of herding. But what is most striking from all this is just how little Banerjee feels he needs to say about the relationship between the model and the real world.

This property of Banerjee’s presentation is entirely normal in the literature of economic modelling. As I show in my 2000 paper, Akerloff’s and Schelling’s accounts of their models have just the same feature. It seems that, within economics, explicit discussion of the relationship between a model and the corresponding real-world phenomena is not required. In the present case, Banerjee describes a real-world phenomenon, namely herding, in general terms. He then constructs a well-specified model world and derives specific conclusions about what happens within it. What we see in the model world is a form of herding, caused by a mechanism of information and signalling. By means of the restaurant story, he links the formal objects of the mathematical model with things in the real world with which we (the readers) are familiar. Very informally, he invites us to consult our experience of restaurants and to conclude that what is going on in his model world is in some way similar to that experience. And that is it: we are left to draw the appropriate conclusions.

From Banerjee’s stated aims, we can infer that we are expected to learn something about real-world herding. That something, presumably, is that real-world herding behaviour is, or at least may be, induced by a mechanism of imperfect information and signalling similar to that exhibited in the model. The model itself provides a stylised description of the mechanism he has in mind, and shows how that mechanism leads to herding behaviour in the world of the model. We are being invited to infer that the same mechanism may be at work in the relevant real-world cases. Given the stylised nature of the model, this ‘may be’ is perhaps best interpreted as a cautious conjecture: Banerjee is trying to convince us that we should take seriously the possibility that his explanation of real-world herding is correct. Still, what we are being asked to take seriously is a hypothesis about the causation of actual events.

How can Banerjee’s model tell us anything, however speculative, about causation in the real world? The implicit argument, I suggest, is abductive. The effect of herding in the model world is similar to that of herding in the real world. From the similarity of effects, we are invited to infer the likelihood of similar causes: the model gives us some grounds for confidence in the hypothesis that real-world herding is caused by a mechanism similar to the one that causes herding in the model. The essential structure of the argument is: from some similarities, infer others. Thus, we can have more confidence in inferences from the model world to the real world, the more similar the two are. Since the model world is so stylised, “is similar to” cannot sensibly be read as “realistically describes”. But we can ask for credibility in the sense that the fictional world of the model is one that could be real. This, I suggest, is where the story of the restaurants comes in. We are expected to be able to imagine the world of the two restaurants, and to think of the information structure and individual motivations of this world as like ones we have experienced in reality.

4 An Example from Biology: Maynard Smith and Price’s Model of Asymmetric Animal Contests

My example from theoretical biology is a classic paper by John Maynard Smith and Geoffrey Parker (1976), “The logic of asymmetric contests”. This was one of the earliest contributions to a literature initiated by Maynard Smith and George Price (1973), which uses a form of game theory to analyse animal behaviour in situations of conflict.3 Typical examples are cases in which two animals of the same species come into conflict over nesting sites, feeding sites or mating opportunities. The general object is to understand how such conflicts are structured and what determines which contestant wins and which loses.

Maynard Smith and Parker (from now on, ‘MSP’) begin their paper by stating their objective: “This paper discusses the question, ‘How would we expect animals to behave in conflict situations?’” Their particular concern is with asymmetric contests—that is, conflicts in which the two contestants occupy asymmetric positions, with the implication that, in principle, the resolution of the conflict could be determined by that asymmetry. MSP distinguish between three types of asymmetry. There is payoff asymmetry if one contestant stands to gain more than the other from victory, or stands to lose less than the other from defeat. There is asymmetry in resource-holding potential if one contestant has greater fighting ability than the other, and so is more likely to be the winner. And there is uncorrelated asymmetry if the contestants differ in some respect which, while capable of being recognised by the contestants themselves, is uncorrelated both with payoffs and with fighting ability. MSP are primarily concerned with this third type of asymmetry.

In principle, a conflict could be resolved by using an uncorrelated asymmetry to determine which contestant is the winner. However, MSP admit that they cannot give any real examples of this form of conflict resolution. In nature, they suggest, the symmetries that are used to resolve contests will almost always be correlated with differences in payoff or fighting ability. But:

It is, however, important to analyse contests which are uncorrelated in the above sense, because if it can be shown that completely uncorrelated asymmetries can settle contests, then the argument that differences in pay-off or RHP [resource-holding potential] are too small to explain the conventional settling of disputes is irrelevant. Thus it is no part of our argument that differences in pay-off and RHP do not exist, only that they need not exist for contests to be settled conventionally (p. 159).

I take it that a contest is “settled conventionally” if it is resolved without significant cost to either contestant, as a result of their both recognising some cue which tells them who should accept defeat. It might seem from this quotation that MSP are setting out to show only that a contest could be resolved by an asymmetric convention. But, as will emerge later, their model is used to support a stronger claim—that if, in a given contest, the only commonly-recognised asymmetry is uncorrelated, then that asymmetry will be used to resolve the conflict.

MSP develop their argument by presenting an extremely simple and apparently unrealistic model of an animal conflict. Their general modelling strategy is to represent animal contests as two-player games, in which strategies represent alternative behaviour patterns and payoffs are measured in units of Darwinian fitness (that is, as changes in the expected number of offspring contingent on the relevant outcome, measured relative to some baseline). The core game (now generally known as Hawk–Dove) has two contestants A and B in conflict over some resource. Each contestant has two alternative pure strategies, escalate (act with increasing aggression until the other contestant backs down or until one contestant is seriously injured) and retreat (back down at the first sign of aggression by the other contestant). The payoff matrix for the game is shown in Table 1. Incremental fitness is measured relative to the outcome of playing retreat against escalate (that is, winning nothing but not having to fight). V is the value of the resource and D is the cost of injury to the loser of a fight; D > > 0, implying that escalate is the best response to retreat and vice versa. The symmetry of the payoff matrix represents the assumption that the asymmetry between A and B is uncorrelated with payoffs or fighting ability; it is assumed that if both contestants escalate, each is equally likely to win the fight, and that if both retreat, each has an equal chance of getting the resource without having to fight. MSP suggest the interpretation that A is the “discoverer” of the disputed resource and that B is the “late-comer”.
Table 1

The Hawk-Dove game


B’s Strategy



A’s Strategy


(– D)/2, (– D)/2

V, 0


0, V

V/2, V/2

> 0

Notice that the specification of the game incorporates some drastic simplifications of real-world animal contests. As I have explained, the symmetry of the payoff matrix is an unrealistic assumption, deliberately introduced by MSP to isolate the mechanism they wish to investigate. The assumption that there are only two levels of aggression simplifies the analysis by transforming a general feature of the real world (in any contest there is a spectrum of alternative behaviours, differing in their degrees of aggression) into a concrete property of the model world. MSP offer no defence of this assumption, simply instructing the reader: “Consider now a contest in which two pure strategies are possible” (p. 161). It is implicit in the specification of the game that both players recognise the asymmetry between A and B. MSP simply state that they are assuming “perfect information”. The real-world asymmetries that they use as illustrations (for example, discoverer versus late-comer, large animal versus small animal) are ones which it seems credible to suppose that animals could use as cues, but presumably it would be more realistic to postulate imperfect information about such asymmetries. MSP implicitly recognise that the perfect information assumption is unrealistic, and defend it on grounds of tractability: “Contests in which there is perfect information available to both contestants are in general rather easy to analyse…Much greater difficulties arise when only partial information exists” (p. 160). Later in the paper they explore some ways of relaxing this assumption (pp. 166–171).

MSP introduce a further set of simplifications by carrying out their analysis in terms of the concept of an evolutionarily stable strategy (ESS), introduced by Maynard Smith (1974). In the first paragraph of their paper, MSP report (and implicitly endorse) Maynard Smith’s argument “that natural selection, acting between individuals, would produce such a strategy [i.e. an ESS]” (Maynard Smith and Parker 1976, p. 159). Roughly, the pattern of behaviour in a population of animals of a given species is an ESS if that population cannot be successfully invaded by any mutant with a different behaviour. However, as MSP explain, this concept of ‘invasion’ is a property of a highly simplified model of natural selection (pp. 160–161). Among the assumptions of this model are the following. First, each mode of behaviour has a distinct genotype. (Thus, the evolution of behaviour can be explained by genetic selection rather than, for example, by developmental or environmental influences on given genotypes.) Second, the genetic determination of behaviour in contests is independent of the determination of the roles A and B. (For example, the probability that a given animal plays the role of discoverer is the same whether it has the escalate or retreat genotype.) The third assumption is so unrealistic that MSP seem reluctant to state it outright.

The concept of an ESS, interpreted literally, applies only to species which reproduce asexually. If there is asexual reproduction, a genotype for behaviour which is successful in terms of Darwinian fitness will, by definition, be successful in creating copies of itself in the next generation. But if reproduction is sexual, there is genetic recombination between generations, and so it is not necessarily true that the fittest genotypes will increase in frequency from generation to generation. As a simple counter-example, consider the case of a behaviour that is determined by two alleles, A and a, for the same genetic locus. There are three relevant genotypes, AA, Aa and aa. The relative frequency of these three genotypes is determined by only one parameter, the relative frequency of A. In particular, the Aa genotype can be generated only in a gene pool which also generates AA and aa genotypes. So if the behaviour induced by Aa maximises Darwinian fitness, we will not observe a population in which all individuals behave in this way.4

MSP approach this issue obliquely, with the opening remark: “A word must be said about the inheritance of behavioural strategies”. They present three alternative forms of inheritance. The first possibility is that “[e]ach strategy, pure or mixed, can reproduce itself without genetic recombination with others”. This is shown to justify the use of ESS models. The second possibility is that only pure strategies can reproduce, and that (as before) reproduction is without recombination. The differences between this and the first possibility are not particularly relevant in the relation to the Hawk–Dove game, in which the interesting ESSs involve pure strategies. The third possibility is the realistic one. All that MSP have to say about this is the following:

(iii) Bisexual inheritance with genetic recombination. Nothing general can be said. There are cases (e.g. the “war of attrition”) in which the ESS calls for a frequency distribution which could not be maintained under sexual reproduction with most types of genetic determination. In such cases, simulation suggests that the genetic equilibrium will approach as close to the ESS as the genetic system allows (p. 161).

In effect, then, MSP are assuming asexual reproduction. This assumption is particularly interesting because, taken at face value, it is neither a limiting case of a property of the real world nor a way of making a general property of the real world more concrete. In a later work, addressed to a more general readership, Maynard Smith (1982) explicitly acknowledges that ESS models assume asexual reproduction, and offers the following justification:

The basic assumption of evolutionary game theory—that like begets like—corresponds to what we actually know about heredity in most cases. To analyse a more detailed genetic model would be out of place. For example, it is relevant to the evolution of wing form that the shape which generates a given lift for the minimum induced drag is an elliptical one. If someone were to say “Maybe, but how do you know that a bird with an elliptical wing is not a genetic heterozygote which cannot breed true?”, he would rightly be regarded as unreasonable (1982, p. 4).

In other words, it is a general practice in biology to use the “like begets like” principle as a default assumption when explaining the broad properties of the products of natural selection, even though it is known not to apply universally. Maynard Smith (1982, pp. 4, 20–22) offers some biological reasons for expecting this assumption to be reasonably accurate, and implies that he believes that it has proved sufficiently reliable in comparable previous cases. Default assumptions of this kind are a common motif in modelling: compare the assumption that firms maximise profit, made in many economic models.

It is now time to consider the use that MSP make of the Hawk–Dove model. The central theoretical result is that the game has two ESSs, “escalate if A, retreat if B” and “retreat if A, escalate if B”. The implication is that, in the world of the model, natural selection will lead to the evolution of a conventional resolution of the conflict. Even though the asymmetry is correlated neither with payoffs nor with fighting ability, it will provide the cue for settling the contest (pp. 163–164).

Having established this result, MSP consider the effects of relaxing some of their assumptions. In the context of their main argument, the most important analysis is of the effects of relaxing the assumption that the asymmetry is uncorrelated. Suppose, for example, that the asymmetry is correlated with payoffs, so that on average A (the ‘discoverer’) stands to gain slightly more from victory than B (the ‘late-comer’). If the difference is payoffs is relatively small, the previous result still holds: there are two ESSs. One of these (which MSP call the common-sense ESS) settles the contest in favour of A; the other (the paradoxical ESS) settles it in favour of B. MSP present a variant model in which the asymmetry between A and B is correlated with payoffs in this way.5 In the initial state of this model, contestants are assumed to ignore the asymmetry between A and B; there is a mixed-strategy ESS in which contestants in both roles sometimes escalate and sometimes retreat. MSP show that this equilibrium can be invaded by a mutant which recognises the asymmetry and plays the common-sense strategy, while it cannot be invaded by a mutant which plays the paradoxical one.

It is only after completing their analysis of these various models that MSP turn to the real world. The final section of the paper (roughly a quarter of the paper in length) is entitled “Discussion”, and explores the implications of the preceding analysis for actual animal contests. This section begins:

Two general conclusions emerge from the preceding analysis, one relevant to symmetric and the other to asymmetric contests. …In asymmetric contests, mixed strategies will be the exception. Usually, some asymmetric feature will be taken as a ‘cue’ by which a contest can be settled conventionally. We shall discuss first whether there is any observational support for these two conclusions (p. 171).

This passage marks the transition from model worlds to the real world. Notice how quick the transition is, and how little is said to explain it. Up to this point, MSP have said almost nothing about real animal contests; they have merely shown us what happens in various model worlds. But they expect the reader to understand that these modelling exercises lead to specific hypotheses about real animal contests—hypotheses for which it may be possible to find “observational support”.

It must be said that MSP’s methodological strategy differs from Banerjee’s (and also from Akerlof’s and Schelling’s) in presenting an explicit empirical hypothesis. However, that hypothesis is stated only in vague terms: asymmetric contests are usually settled conventionally, even when differences in payoffs and fighting ability are small. There is no explanation of how this general hypothesis is derived from, or supported by, the model; it simply “emerges”. And, although the “Discussion” section refers to substantial empirical work on animal behaviour, MSP do not attempt to test their general hypothesis. (Indeed, it is not clear how it could be tested.) Instead, and like Banerjee, Akerlof and Schelling, MSP point to an array of real-world cases in which observed behaviour resembles behaviour in their models.

In relation to asymmetric contests, the relevant discussion of real-world evidence comes in a subsection entitled “Are conventional cues used in nature to settle asymmetric contests?” (pp. 172–173). MSP marshal a body of evidence about asymmetric contests in nature. A typical example concerns competition between male swallowtail butterflies for the hilltop territories that females visit in search of mates. It has been observed that contests between males are normally settled very quickly in favour of the first occupant. Noting that there is “no obvious reason” to expect first arrival at a hilltop to be correlated with payoffs or fighting ability, MSP cautiously suggest that this is “an example of an uncorrelated asymmetry being used to settle a contest”.

A further subsection of the “Discussion” deals with paradoxical ESSs (p. 174). This subsection differs from the one on conventional cues in not presenting real-world evidence. Instead, it proposes a hypothesis about the real world: “it is unlikely that paradoxical ESSs occur in nature”.6 MSP defend this hypothesis by referring back to the model of an asymmetry that is initially ignored, in which the initial equilibrium can be invaded only by the common-sense ESS. Here again, we see a very quick transition from a property of the model world to the hypothesis that the real world has a similar property.

MSP’s methodological strategy is, I suggest, broadly similar to that of Banerjee, Akrelof and Schelling. In each of these four papers, the central contribution is a theoretical model (or set of models). Each model is a fully-specified, self-contained and counterfactual world. The authors show that (human or animal) behaviour in their models is governed by certain mechanisms or exhibits certain regularities. We, the readers, are invited to conclude that we have been given some additional reason to believe that mechanisms or regularities similar to those in the models will be found in the real world; but the authors seem reluctant to say what that reason is. Although the model world and the real world are both discussed, very little is said explicitly about the relationship between one and the other.

5 Credible Worlds

In economics (and perhaps, as the example from biology suggests, in other sciences too) there seems to be a convention that modellers need not be explicit about what their models tell us about the real world. Given this convention, it is hardly surprising that the question of what role models play in economics is controversial among methodologists. However, that convention may also provide clues for answering the methodological question. A satisfactory account of the role of models, I submit, needs to be consistent with the fact that economists do not find this convention awkward or constraining. I think that my account of models as credible worlds helps us to understand what is going on.

One of my motivations for writing the 2000 paper was my sense of a mismatch between how economic theorists understood their models and how modelling was understood in (what were then) the most influential traditions of economic methodology. I now realise that, at around this time, philosophers of science and methodologists of economics were beginning to reappraise former ideas about the role of models. One significant theme, developed by Margaret Morrison and Mary Morgan (1999), was that models have an autonomous status, independent of both theory and the world, by virtue of which they can help us to learn about theory, help us to learn about the world, and mediate between the two. In a broad sense, my paper was an exploration of some of these potentialities of models.

There are closer connections between my paper and Roland Giere’s (1988) account of scientific explanation. Giere characterises a scientific theory as comprising a set of related models and a set of hypotheses linking those models with systems in the real world. A model is an abstract entity, created by the scientist, possessing exactly the properties that the scientist stipulates. In itself, it makes no claims about the world. Hypotheses assert similarities between the model and the world. Giere’s central example is Newtonian mechanics. For Giere, this theory has a family of models with the “common general schema” that force equals mass multiplied by acceleration. One such model is the two-particle gravitational system in which force is related to distance and mass by Newton’s inverse square function. The relative motions of the two particles in this model are properties of the model and nothing more. But the theory includes hypotheses such as that the relative motions of the earth and moon are very similar to those of particles in the model (pp. 62–91). On this account, a model is a construction, not a stripped-down description of the world. In investigating the properties of a model, that is all we are doing: we are not deducing the effects of known laws in controlled or idealised real-world systems. There is a sharp conceptual distinction between that activity and the investigation of similarities between the model and the world.

The credible worlds account is based on a similar understanding of what models are. It is essential to this account that the model world is a construction of the modeller, with no claim to be anything other than this. Its specification is just whatever the modeller has chosen it to be. In particular, there is no claim that it has been constructed by stripping out some features of the real world and describing what remains. In contrast, a model constructed in the latter way is, at least in principle, an isolation in the following strong sense: by virtue of the method of construction, it describes some aspect of reality, isolated from other factors. The properties of such an isolating model, properly understood, are therefore also properties of the real world. This is the sense of ‘isolation’ that I read into Mäki’s (1992, 1994) early work on the “method of isolation” in economics.

I now think that in my 2000 paper, my picture of the stripping-out process involved in this strong form of isolation was too literal-minded. As Mäki (2009) points out, just about any practical attempt to isolate a real-world process will involve adding something. For example, if we want to run a controlled experiment to isolate the effects of different amounts of sunlight and water on the growth of plants, we will need some common medium in which to grow our plants. Suppose we use some standard, artificially sterilised compost mix. Then, in constructing the experiment, we are not just stripping out naturally-occurring differences in soil composition; we are introducing a new composition. Still, the experiment is an exercise in isolation. For the same reasons, modelling isolation may require the specification of a standardised environment in which the mechanisms to be studied can operate. For example, and contrary to an argument in my 2000 paper, the checkerboard form of Schelling’s model cities might be interpreted in this way. However, I stand by the claim that, at least in economics, theoretical models are typically not isolations in the strong sense. I will say more about this in Sect. 5, when I discuss Cartwright’s account of modelling.

If the concepts of a model are given ordinary-language labels, and if the workings of the model make rough intuitive sense in terms of those labels, it is possible to talk about a model world. As I argued in Sect. 1, most economic models have this property. So does MSP’s biological model. Given that a model world can be described in this way, we can assess its credibility. Credibility is not the same thing as truth; it is closer to verisimilitude or truthlikeness. We perceive a model world as credible by being able to think of it as a world that could be real—not in the sense of assigning positive subjective probability to the event that it is real, but in the sense that it is compatible with what we know, or think we know, about the general laws governing events in the real world. In my 2000 paper, I offer the analogy of credibility in realistic novels, which is developed by Till Grüne-Yanoff (2009). Mäki’s (2009) “way the world works” constraint expresses a similar idea.

As Xavier de Donato Rodríguez and Jesús Zamora Bonilla (2009) point out, the idea that a credible world “could be real” cannot be taken too literally (as perhaps it was in my 2000 paper). Economic models often contain idealisations which, if interpreted literally, cannot be true. Continuity assumptions are a case in point: economists routinely model integer-valued concepts as if they were continuously variable. For most economists, this kind of idealisation is so normal a part of modelling that it is barely noticeable. We know (or think we know) that continuity assumptions do not materially affect the results we can derive, while making the analysis much more tractable. When we think about the credibility or non-credibility of a model, we mentally remove such idealisations and imagine the corresponding integer-valued world.

One crucial difference between a credible world and an isolation is that a credible world may be constructed around general empirical regularities—one might say, empirical laws—that are merely postulated. For all we know, these regularities may not be part of how the world really works. All that is required is that, in the current state of knowledge, they are credible candidates for truth.

An illuminating example of this kind of credible world is described by Giere (1988, pp. 249–252), who is my source for the following material. From the 1920s to the early 1960s, the hypothesis of continental drift, first proposed by Alfred Wegener, was controversial in geology. On the one hand, there was a large body of evidence of geological, paleontological and biological correspondences between widely-separated continents, all of which was consistent with the hypothesis that previously contiguous land masses had broken up and drifted apart. On the other, there seemed to be no physical mechanism which could move continental masses such enormous distances. In the late 1920s, Arthur Holmes suggested a possible answer, in the form of a sketch of a model in which convection currents in molten material below the earth’s crust create a conveyor-belt effect which can drag continents apart. Holmes had almost no positive evidence for what he later called “a purely hypothetical mechanism”, although he thought it compatible with what were then recent discoveries about radioactive heating within the earth. One of the main opponents of the continental drift hypothesis, Harold Jeffreys, acknowledged that, as far as he could see, there was “nothing inherently impossible” in this mechanism, while remaining unconvinced of its likely reality. Holmes’s model, I suggest, is a credible world. In terms of the conceptual structure I introduced in Sect. 1, this model relies heavily on substantive assumptions whose truth value is unknown (at the time it is put forward). However, it generates results which are consistent with known properties of the real world—properties that other theories cannot explain. The model is used to support the conjecture (subsequently confirmed) that a mechanism similar to that of the model is operating in the real world. Notice that Holmes’s argument has the same abductive structure as Banerjee’s.

A common theme in many criticisms of the credible worlds approach is to question the validity of the modes of inference—abduction, or other suspect forms of induction—that it attributes to modellers’ reasoning. Explicitly or implicitly, Aydinonat (2007), Cartwright (2009) and Grüne-Yanoff (2009) all appeal to tightly-restricted canons of inductive inference whose effect is to confine modellers within the structure of argument that characterises the isolation approach, as outlined in Sect. 1.7 I stand by the arguments of my 2000 paper: this structure of argument is too restrictive to encompass the inferences that modellers want to make, and are justified in making.

It may help to explain my position to say that, when I use concepts like ‘justification’, I am not claiming to contribute to the enterprise in which philosophers of science explicate abstract principles by which claims to knowledge or belief can be rationally grounded. My approach is both more naturalistic and more pragmatic. My aim is to investigate the modes of reasoning that economic theorists use in their work, and to assess whether these are effective in helping them to understand real economic phenomena.8 Since we all find it necessary to use inductive inferences in our everyday lives, it should not be surprising to find that these are part of the practice of science too—however problematic they may for professional logicians.

6 Models as Isolating Tools

Cartwright (1998, 2002) offers a different account of the role of models in economics, dovetailing with her conception of the nature of scientific knowledge. For Cartwright, the world as we confront it “is for the most part both messy and arbitrary and not the sort of thing about which the kind of knowledge we call scientific is possible” (2002, p. 137). Scientific laws—invariant associations between events—are not the fundamental fabric of nature. Laws operate only in very special circumstances, in which particular causal factors work together in particular configurations, isolated from other disturbing factors. Science works by discovering or constructing such configurations or nomological machines. In the era of Galileo and Newton, the solar system served as a natural nomological machine for the study of gravity. Galileo’s experiments with inclined planes exemplify the use of a constructed nomological machine. Cartwright argues that models in economics serve the same purpose for the study of capacities in the economic world, and proposes the following account of how we can use models to learn about capacities:

For the model to succeed in showing that a factor C has the capacity to produce E we must be in a position to argue that (a) the specific features incorporated into the model do not interfere with C in its production of E… Beyond that, (b) these features must be detailed enough for it to be determinate whether E occurs or not; and (c) they must be simple enough so that, using accepted principles, we can derive E. Finally, and most difficult to formulate, (d) the context must be ‘neutral’ to the operation of C, allowing E to be displayed ‘without distortion’…If conditions (a) to (d) are satisfied, we may say that we have a theoretically grounded hypothesis about the capacity. The capacity would be expected to be stable across the range of circumstances where the general principles and the assumptions about interference and neutral context are valid (1998, pp. 45–48).

It is crucial to this account that a model purports to isolate a mechanism which, given the right initial conditions, operates in the world at large. By this, I do not mean merely that the model exhibits this mechanism working in isolation in an imaginary world, while leaving open the question of whether any similar mechanism operates (perhaps alongside others) in the real world. For example, it seems uncontroversial that Banerjee’s model exhibits a herding mechanism in the sense that it describes a world in which such a mechanism is at work, and that the model has been constructed to exclude many other mechanisms that might operate in the real world.9 Cartwright intends more than this. For her, the function of a model is to demonstrate the reality of a capacity by isolating it—just as Galileo’s experiment demonstrates the constancy of the vertical component of the acceleration of a body acted on by gravity. Notice how Cartwright speaks of showing that C has the capacity to produce E, and of deriving this conclusion from accepted principles. A satisfactory isolation, then, allows a real relationship of cause and effect to be demonstrated in an environment in which this relationship is stable. In more natural conditions, this relationship is only a latent capacity which may be switched on or off by other factors; but the capacity itself is stable across a range of possible circumstances. Thus, the model provides a “theoretical grounding” for a general hypothesis about the world.

As an example of this kind of modelling, consider the mathematical models that structural engineers use when designing buildings. These models represent (what from an engineering perspective are) the most relevant features of structures in a form which allows the application of well-established engineering principles, such as those of Newtonian mechanics. The conclusions that are derived are theoretically grounded in Cartwright’s sense (they have been derived by valid reasoning from accepted principles), while being true only in an other-things-being-equal sense. For example, some kinds of engineering model can show that a structure will support itself without collapsing under its own weight, while saying nothing about whether it would survive the vibration of an earthquake. A model of this kind can plausibly be understood as a tool for discovering capacities that operate in the real world.

But if we try to interpret Banerjee’s paper in terms of this account of models, we hit what I think is a fatal problem: Banerjee does not propose any explicit, general hypothesis about the world. As I show in my 2000 paper, the same is true of Akerloff’s and Schelling’s arguments. If the whole point of model-building is to ground hypotheses about capacities, why do these celebrated exercises in modelling not tell the reader what hypotheses are being grounded?

The most obvious answer is that these models cannot be used to ground hypotheses in the way that Cartwright’s account of modelling requires. Just about all the significant features of Banerjee’s model are ones that he has chosen to impose; they are not (as the principles of mechanics are) accepted principles about empirical reality. The conclusions that can be derived from Banerjee’s model, using standard principles of deductive logic, are not hypotheses but theorems.

Cartwright (2009) recognises that this is a characteristic feature of economic models, but thinks that this fact counts against economics rather than against her account of modelling. Maintaining that “[i]deally besides the specific description of the cause whose capacities we study, the only premises in use [in a model] should be general principles and assumptions that guarantee that the experiment is indeed Galilean” (Sect. 4), she concludes that it is “especially troubling” for economics that there are so few “acceptable principles” of the required kind (Sect. 1).

Similar problems arise, if not quite so starkly, if we try to apply Cartwright’s account to MSP’s Hawk–Dove model. Unlike Banerjee, MSP do propose a general hypothesis about the world, namely that in nature, asymmetric animal contests are usually resolved conventionally. But the “emergence” of this hypothesis from the model hardly satisfies Cartwright’s conditions for a satisfactory theoretical grounding. The Hawk–Dove model does make use of some accepted principles of biology—the principles of Darwinian natural selection. But the workings of those principles are explored in a counterfactual world created by MSP. Many of the features that have been built into that world—for example, asexual reproduction and the entirely genetic determination of behaviour—seem to be modelling conventions rather than accepted principles or neutral specifications of ‘context’. This makes it hard to make sense of the idea that the model isolates an other-things-being-equal tendency that is at work in real-world cases such as that of the swallowtail butterflies. Suppose one tries to find a general description of the mechanism that generates MSP’s results. My attempts end up with propositions such as the following: “In any two-player game with the Hawk–Dove payoff structure and in which there is common knowledge of an uncorrelated asymmetry, there are exactly two ESSs, each of which uses the asymmetric cue to resolve the conflict”. Such propositions do not describe real causal mechanisms that can be discovered by simulating Galilean experiments: they are theorems that are true by virtue of the principles of mathematics and logic.

There are interesting parallels between the Hawk–Dove model and one of Cartwright’s (1998, 2002) favourite examples of economic modelling—the labour-market model constructed by Christopher Pissarides (1992). Pissarides’s model, like the Hawk–Dove model, is used to support a general hypothesis about the real world. Pissarides presents his model as an explanation of the persistence of negative “employment shocks”. The essential idea is that workers’ skills deteriorate during episodes of unemployment, and that a deterioration in the average skill level makes firms less willing to create jobs in subsequent periods. The model is a complex structure of inter-related components—overlapping generations of workers, a random process for matching potential workers to jobs, Nash bargaining between matched workers and firms, and so on. Pissarides shows that, within this model, employment shocks can persist. Cartwright sees the complexity of Pissarides’s model as supporting her thesis that models are nomological machines: “That is the trick of building one of these economic models: you have to figure out some circumstances that are constrained in just the right way that results of interest can be derived deductively” (2002, p. 147).

Unlike Banerjee, Pissarides ends his paper with a section devoted to “empirical implications”. He presents this part of the paper as “going beyond” the highly stylised model in which the result was derived; it describes “the empirical model that is implied by the analysis [of the theoretical model]” (p. 1387). This empirical model is a system of two equations, expressing relations between labour-market variables such as unemployment, vacancies and search intensity. The idea is that the empirical model can be estimated econometrically, using data from real labour markets; by these means, its real-world explanatory power can be tested. On Cartwright’s account, Pissarides’s empirical model is the general hypothesis that is grounded in the theoretical model.

The difficulty here is with the idea of “grounding”. Or, to put this another way, it is with fulfilling Cartwright’s condition (d). The array of assumptions that specify the theoretical model are, as Cartwright says, configured to allow the persistence result to be derived. But the empirical model is intended to be estimated using data from real labour markets, in which those assumptions are clearly not satisfied. The empirical model treats the real labour market as if it were the labour market of the model. If the empirical model is to inherit the deductive grounding of the theoretical results, we need some way of demonstrating that a result that has been derived under a particular set of finely-tuned assumptions holds in the messy conditions of the real world. Of course, it would be nice to be able to do this: as Cartwright puts it, “we want our treatments to be rigorous and our conclusions to follow deductively” (2002, p. 147). But wanting something does not make it possible.

When Pissarides speaks of “going beyond” the theoretical model, I take him to be saying that this step involves something less strict than deduction. The sense in which the empirical model is grounded on the theoretical one might be expressed by saying that the one is inspired by the other, or that the theoretical model gives us some grounds for confidence in the implications of the empirical one. I cannot see what more can be said than this.

7 Social Mechanisms

The difficulty of justifying such steps of argument might be avoided altogether by claiming that theoretical models do not tell us anything about the real world. It might be said that a model tells us only that if a certain set of conditions—those built into the specification of the model—were to hold, then a certain set of effects—the ‘results’ of the model—would occur. Of course, empirical propositions can be stated as material implications with the ifthen…form; and if models are understood as isolating tools, this is just the kind of empirical proposition that they will generate. (For example: If a body is placed on a frictionless inclined plane at the surface of the earth, the vertical component of its downward acceleration will be 9.8 m/s2.) But if all the specifications of the model are included in the if…part of a proposition, that proposition is not a material implication whose truth is a matter of contingency; it is a necessarily true theorem. There is a sense in which such propositions can be read as asserting the possibility of particular mechanisms or capacities, but only if ‘possible’ is interpreted as ‘conceivable’ or ‘logically possible’, rather than as supporting a belief or conjecture about the real world. To interpret models as generating theorems is to treat modelling as conceptual exploration. As I have already said, my observations have led me to the conclusion that many economic theorists do think of modelling in this way.

Aydinonat (2007) and Grüne-Yanoff (2009) both propose this kind of interpretation of Schelling’s model, arguing that it is intended only to tell us about what effects would occur, were all the assumptions of the model to hold. de Donato Rodríguez and Zamora Bonilla (2009, Sect. 4) propose a similar interpretation of Akerlof’s model, arguing that it is intended only to show “how to model” a class of market situations and to point the direction for a new research programme. As I acknowledge in my 2000 paper, there are passages in Schelling’s and Akerlof’s texts which suggest that they are inclined to favour this interpretation of their own work. The same might be said of MSP’s remark, quoted in Sect. 3, that “it is no part of our argument that differences in pay-off and RHP do not exist, only that they need not exist for contests to be settled conventionally”. My claim, the supporting arguments for which are in my 2000 paper, is that these authors’ extensive discussions of real-world evidence make sense only if they believe that their models are capable of telling us something, however speculative, about the real world.

Given the role that his checkerboard model has come to play in methodological discussion, it is particularly interesting to consider Schelling’s (2006, pp. 235–248) own methodological account of “social mechanisms”. He gives the following definition: “[A] social mechanism is a plausible hypothesis, or set of plausible hypotheses, that could be the explanation of some social phenomenon, the explanation being in terms of interactions between individuals, or between individuals and some social aggregate” (p. 236). His main example is the logistic function. Many dynamic phenomena follow logistic curves. Examples include the spread of infectious diseases and the diffusion of new technologies. The logistic function itself is not a social mechanism (it is just a mathematical expression). Nor is the fact that certain data fit a logistic curve (that is just an unexplained fact). But this fact “invites explanation” in terms of a social mechanism. Schelling takes the example of an observed logistic relationship for the sales of a novel. He asks us to consider a mechanism in which a population of individuals are in one of two states—‘infected’ people who have read the book and ‘uninfected’ people who have not. When an infected individual comes into contact with an uninfected one, there is some probability that the latter becomes infected. If contact between individuals is random, the relative frequency of infection over time follows a logistic curve. Thus, the mechanism generates a pattern similar to that found in the sales data: “it is a mechanism that can account for what we have observed” (pp. 236–238).

Schelling then asks what we gain by proposing social mechanisms as explanations for empirical regularities. Among his answers is the following: “[O]nce we see the mechanism, how it works, and maybe its mathematical shape, we have a kind of template that may fit other phenomena” (p. 240). This is clearly true of the infection mechanism which generates the logistic function. As another example, Schelling refers to the predator-prey relationships in ecology modelled by the Lotka-Volterra equations. It is easy to think of further examples of mathematical structures which apply to a wide range of real-world phenomena by virtue of similarities in underlying mechanisms. I would nominate the concept of mixed-strategy equilibrium in games, apparently first discovered by John von Neumann in relation to bluffing in poker. Schelling is too modest to say this, but the mechanism of his segregation model undoubtedly fits the bill. So do Akerloff’s ‘lemons’ mechanism, Banerjee’s herding mechanism, and the mechanism displayed in MSP’s Hawk–Dove model, by which games of conflict are resolved by asymmetric cues.

Notice that Schelling presents the process of discovering mechanisms as beginning with an attempt to explain previously observed empirical regularities—to “account for what we have observed”. That fits with my 2000 reading of his segregation model as supporting the conjecture that real-world segregation is caused by a mechanism something like that of the checkerboard model. (Again, the support comes by way of abductive inference.) But Schelling’s discussion of mechanisms as templates implies that a model can be useful in domains that are far removed from the one for which the model was first designed. If that is so, does it really matter whether the model, when first presented, is credible as an explanation of anything in particular? For example, take the case of mixed-strategy equilibrium. The usefulness of this concept in explaining phenomena in economics does not depend on whether von Neumann’s analysis of poker gives a satisfactory explanation of the behaviour of poker players. What matters, one might say, is that von Neumann characterised a social mechanism which turned out to underlie a wide range of empirical regularities, most of which he had probably never even thought of. So what is wrong with presenting a model only as a template, without claiming actually to explain anything?

The most obvious objection is that this makes things too easy for theorists. Consider an analogy: would you buy a tool from a salesperson who assured you that it was likely to be useful to you around the home, but couldn’t specify any way of actually using it? This analogy might suggest that, when a theorist makes links between a model and the real world, these links are merely selling points. By this I mean that the methodological status of the model is as conceptual exploration: what is being offered is a theoretical tool, not an explanation of any particular real-world phenomena. To demonstrate the potential usefulness of the tool, however, the modeller is expected to provide some suggestions about the kind of uses to which it might be put. I have to say that many economic theorists do seem to think of their models in this way: they see their conceptual exploration as the serious content of their work, and the rest as a form of marketing.

At first sight, an account of this kind might seem to explain how theorists can present their models in relation to familiar real-world phenomena (prices of used cars, racial segregation in American cities, the relative popularity of different restaurants) while being so imprecise about what the models tell us about these phenomena. But, even if we are willing to allow a model to be accepted as valuable in the absence of any known useful application, this account runs into a problem. If there is to be a genuine demonstration of the potential usefulness of a theoretical tool, we have to be shown that it works. Continuing with the analogy, think of the old-style vacuum-cleaner salesman who scatters dirt on the carpet and then shows how successfully his product can clean up the mess. If this demonstration is to be at all convincing, the would-be buyer has to believe that the dirt is real dirt and the cleaning is real cleaning. Similarly, if the theorist is offering a tool that is intended to be used in explaining real-world phenomena, a convincing demonstration must display the tool explaining something. Just as the salesman’s dirt is a contrived cleaning problem, chosen to engage the attention of the would-be buyer, so the theorist might choose as the focus of her demonstration some phenomenon that will attract the attention of her readers. (For the academic economists whose attention Banerjee is seeking, choice among restaurants and choice among research topics are presumably engaging topics.) But the theorist still has to produce a real explanation of the phenomenon.

My starting point was a puzzling feature of papers which report exercises in economic (and biological) modelling: that authors typically say very little about how their models relate to the real world. It seems to be seen as sufficient to describe the properties of the model world in parallel with those of the real world, and to point to similarities between the two. The most natural interpretation of this practice is that, in the relevant scientific community, this counts as explanation. If this interpretation is correct, we can understand why theorists who are demonstrating the usefulness of the modelling tools they have invented can do so while saying very little about how their models relate to the real-world phenomena that figure in the demonstrations. But if not, not.

I have suggested that one should be sceptical whenever a theorist claims to have discovered a significant social mechanism, but is unable to give a concrete example of how that mechanism can be part of an explanation of some real-world phenomenon; and I stand by that. In the light of Schelling’s argument about social mechanisms, however, I cannot claim that theorists who make such claims are necessarily committing methodological errors or failing to act in good faith. It is just that the approach of looking for significant mechanisms while not trying to explain anything in particular seems unlikely to be productive.

But in any case, such an approach can do no more than define a demarcation between the job descriptions of theoretical and applied researchers. Perhaps a theorist is entitled to present a model in the hope that it will prove useful, without being able to say how. Still, a model cannot prove useful unless someone uses it, and whoever that person is, he or she will have to bridge the gap between model world and real world. Pissarides’s work illustrates this point. Within the conventions of economics, Pissarides the theorist might well have ended his paper without including the section on “empirical implications”. That shorter paper might have been understood as a contribution to economic theory, not making any specific claims about real labour markets. But if we then try to imagine how that model could be used, we find we need someone to do what Pissarides the applied economist starts to do under the heading of “empirical implications”—namely, to advance the hypothesis that some part of the real world works like the model. And if the model is supposed to give us confidence in that hypothesis, we are entitled to ask how it does so. There is still a gap to be crossed, and that requires inductive inference.


  1. 1.

    I now regret the passages in Sugden (2000, p. 12) in which I claim that the modelling strategies of Akerlof and Schelling are clearly realist.

  2. 2.

    I say more about abduction in Sugden (2000, pp. 19–20). Following Mill (1843/1967, p. 186), I interpret ‘induction’ to include any mode of reasoning which takes us from specific propositions to more general ones. This makes abduction a sub-category of induction.

  3. 3.

    As an economist, I have a natural interest in this particular branch of theoretical biology. However, it would be a mistake to think of this literature as importing into biology a modelling strategy from economics. Initially, game-theoretic modelling in biology and in economics developed independently of one another (see Maynard Smith 1982, p. 10). In the 1970s, most economists interpreted game theory as the analysis of strategic interaction between perfectly rational players. The evolutionary interpretation of game theory, now fashionable in economics, began as an import from biology, drawing heavily on the work of Maynard Smith and his collaborators (e.g. Sugden 1986).

  4. 4.

    This issue is discussed by Maynard Smith (1982, pp. 4, 20–22).

  5. 5.

    In MSP’s paper, this analysis is framed in terms of a different model of conflict, the “War of Attrition”; but the arguments apply with equal force to the Hawk–Dove game.

  6. 6.

    Later, Maynard Smith (1982, pp. 85, 96) became aware of a few cases of what appear to be paradoxical ESSs in nature. He interprets the rarity of these cases as supporting the hypothesis that paradoxical ESSs are possible but unlikely.

  7. 7.

    Cartwright (2009) is particularly uncompromising in her rejection of what she sees as ungrounded inductive arguments. Most commentators on Schelling’s model accept that the mechanism it exhibits is highly robust in the domain of models (see, for example, the literature survey in Aydinonat 2007). Cartwright disagrees, on the following grounds. Given Schelling’s basic assumption that individuals prefer not to live in neighbourhoods in which their own colour is significantly outnumbered, segregated neighbourhoods evolve; this result is robust to different specifications of the space in which they interact. But if instead we assume that individuals always prefer more integration to less and are indifferent between being in the majority and being in the minority, the resulting patterns of segregation or integration are different for different specifications of the space (Pancs and Vriend 2007). Since this latter assumption is wholly different from Schelling’s, and leads to a very different system of dynamics, I cannot see how Schelling’s conjectures are called into question.

  8. 8.

    In this respect too, my approach is similar to Giere’s: see, e.g., Giere (1988, pp. 1–12, 22–28).

  9. 9.

    I take Mäki (2009) to be using the concept of ‘isolation’ in this weaker sense when he says that, in his “MISS” account, models are depicted “in terms of isolations and idealisations”.



Previous versions of this paper were presented at a symposium on economic models at the 2006 Philosophy of Science Association conference in Vancouver and at a workshop on “Models as Isolating Tools or as Credible Worlds?” at the University of Helsinki in 2008. I thank participants in those meetings, and Emrah Aydinonat and an anonymous referee, for comments. The idea of using Banerjee’s model as an illustration was suggested by Maya Elliott. My work was supported by the Economic and Social Research Council of the UK (award no. RES 051 27 0146).


  1. Akerlof, G. (1970). The market for ‘lemons’: Quality uncertainty and the market mechanism. Quarterly Journal of Economics, 84, 488–500.CrossRefGoogle Scholar
  2. Aydinonat, N. E. (2007). Models, conjectures and exploration: An analysis of Schelling’s checkerboard model of residential segregation. Journal of Economic Methodology, 14, 429–454.CrossRefGoogle Scholar
  3. Banerjee, A. (1992). A simple model of herd behavior. Quarterly Journal of Economics, 107, 797–817.CrossRefGoogle Scholar
  4. Cartwright, N. (1998). Capacities. In J. Davis, W. Hands, & U. Mäki (Eds.), The handbook of economic methodology (pp. 45–48). Cheltenham: Edward Elgar.Google Scholar
  5. Cartwright, N. (2002). The limits of causal order, from economics to physics. In U. Mäki (Ed.), Fact and fiction in economics (pp. 137–151). Cambridge: Cambridge University Press.Google Scholar
  6. Cartwright, N. (2009). If no capacities then no credible worlds. But can models reveal capacities? Erkenntnis, this issue. doi:10.1007/s10670-008-9136-8.
  7. de Donato Rodríguez, X., & Zamora Bonilla, J. (2009). Credibility, idealisation, and model building: An inferential approach. Erkenntnis, this issue. doi:10.1007/s10670-008-9139-5.
  8. Giere, R. (1988). Explaining science. Chicago: University of Chicago Press.Google Scholar
  9. Grüne-Yanoff, T. (2009). Learning from minimal economic models. Erkenntnis, this issue. doi:10.1007/s10670-008-9138-6.
  10. Hausman, D. (1992). The inexact and separate science of economics. Cambridge: Cambridge University Press.Google Scholar
  11. Mäki, U. (1992). On the method of isolation in economics. Poznań Studies in the Philosophy of Science and the Humanities, 26, 316–351.Google Scholar
  12. Mäki, U. (1994). Isolation, idealization and truth in economics. Poznań Studies in the Philosophy of Science and the Humanities, 38, 147–168.Google Scholar
  13. Mäki, U. (2009). MISSing the world. Models as isolations and credible surrogate systems. Erkenntnis, this issue. doi:10.1007/s10670-008-9135-9.
  14. Maynard Smith, J. (1974). The theory of games and the evolution of animal conflicts. Journal of Theoretical Biology, 47, 209–221.CrossRefGoogle Scholar
  15. Maynard Smith, J. (1982). Evolution and the theory of games. Cambridge: Cambridge University Press.Google Scholar
  16. Maynard Smith, J., & Parker, G. (1976). The logic of asymmetric contests. Animal Behaviour, 24, 159–175.CrossRefGoogle Scholar
  17. Maynard Smith, J., & Price, G. (1973). The logic of animal conflicts. Nature, London, 246, 15–18.CrossRefGoogle Scholar
  18. Mill, J. S. (1843/1967). A system of logic. London: Longman.Google Scholar
  19. Morrison, M., & Morgan, M. (1999). Models as mediating instruments. In M. Morgan & M. Morrison (Eds.), Models as mediators: Perspectives on natural and social science (pp. 10–37). Cambridge: Cambridge University Press.Google Scholar
  20. Pancs, R., & Vriend, N. (2007). Schelling’s spatial proximity model of segregation revisited. Journal of Public Economics, 91, 1–24.CrossRefGoogle Scholar
  21. Pissarides, C. (1992). Loss of skill during unemployment and the persistence of employment shocks. Quarterly Journal of Economics, 107, 1371–1391.CrossRefGoogle Scholar
  22. Schelling, T. (1978). Micromotives and macrobehavior. New York: Norton.Google Scholar
  23. Schelling, T. (2006). Strategies of commitment and other essays. Cambridge, MA: Harvard University Press.Google Scholar
  24. Sugden, R. (1986). The economics of rights, co-operation and welfare. Oxford: Blackwell.Google Scholar
  25. Sugden, R. (2000). Credible worlds: The status of theoretical models in economics. Journal of Economic Methodology, 7, 1–31.CrossRefGoogle Scholar

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© Springer Science+Business Media B.V. 2009

Authors and Affiliations

  1. 1.School of EconomicsUniversity of East AngliaNorwichUK

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