In a paper published in Nature in 1995, Steven Frank proposed a simple model to show how “mutual policing” can suppress competition and ensure “fairness” in reproduction, in the evolution of cooperative groups. Twenty-two tears after the paper was published. I asked Steven Frank about his motivation to do the work presented in this paper, the influence of this paper on his subsequent research, and his advice to a reader who is reading his 1995 paper today. Here is what he had to say.
Citation: Frank, S. A. (1995). Mutual policing and repression of competition in the evolution of cooperative groups. Nature, 377(6549), 520.
Date of interview: Questions sent by email on 29th December 2017; responses received by email on 31st December 2017
Steven Frank:This article reflected many of the research trends of evolutionary theory in the 1980s and early 1990s. To set the background, I will describe some of the ideas floating around at that time. I will also mention how my own interests developed from those ideas and set my future course of research. For convenience, I refer to the 1995 Nature article as N95.
The N95 article developed from the problem of how complex sociality and highly cooperative groups could evolve from lower level components. Ultimately, how can new, higher level units originate from lower level units? Recall that Maynard Smith and Szathmary published their Major Transitions in Evolution book in 1995. In the years before that, the processes by which new higher level units evolved was an obscure subject, followed by very few people. I think of Leo Buss, Egbert Leigh, Richard Alexander, Eros Szathmary, Manfred Eigen, John Maynard Smith, and a few others. Although some of their articles and books were known and discussed, the deeper unsolved issues and their significance were truly understood by very few theoreticians.
Obviously, high coefficients of relatedness would lead to nearly unitary behavior of a group. In other words, kin selection of nearly clonal groups would lead to group cohesion. But it was clear that complex sociality and essentially unitary behavior of groups sometimes arose from genetically mixed groups. So, kin selection seemed insufficient for many important cases. That problem was well understood and widely discussed with regard to the origin of sociality in insects, with review articles and summaries appearing in the mid-1980s.
In addition to social insects, the transition of humans to increasingly larger and more complex social groups, in spite of likely genetic heterogeneity, was emphasized by Richard Alexander in his 1979 and 1987 books. Eigen and Schuster discussed the problem of how cells came to be cohesive units, given that they must have arisen from collections of sometimes heterogeneous genetic components.
Leo Buss’s book, The Evolution of Individuality, focused on the problem of how a large number of cells could form a cooperative, unitary multicellular individual. With a large number of cells in a body, there could be enough somatic mutation to break down the sufficiency of kin selection acting alone, and so it seemed like some other process must also be at work in maintaining cooperation.
There were many ideas about supplemental processes to kin selection. But no process had been identified that was sufficiently general. So the broad problem of cooperative groups and the origin of higher level units was unsolved. That unsolved problem is what eventually led to my N95 article.
All of that was going on in the 1980s. I was following those ideas, because much of my work at that time concerned kin selection theory. My interests arose from my field studies of fig wasp sex ratios. That field work led to my theoretical interest in sex allocation with competition between genetic relatives for access to mates or resources. In the mid-1980s, kin selection theory was widely known and thought of by most empirically minded biologists as fully developed. However, kin selection theory as it existed then could not be used to solve simple sex allocation problems of local mate competition or local resource competition or simple problems of dispersal when relatives compete. Hamilton himself typically did not use kin selection theory to solve problems of sex allocation or dispersal. Instead, he used traditional population genetic methods. After he found solutions by traditional methods, he would then offer interpretations in terms of kin selection.
My theoretical work in the 1980s developed kin selection theory into a tool that could be used to solve actual problems of sex allocation, dispersal, and eventually many other common scenarios of social interaction. So I was very much tuned in to the problems of social evolution theory of that time, including debates about kin selection and group selection.
By 1987, I was mostly finished with that development of kin selection into a useful and widely applicable method of analysis. A couple of years earlier, I had started my second main project of those years, what could be broadly called coevolutionary genetics. The problems included host-parasite interactions and the genetics of conflict between different parts of a genome. I also become interested in many microbial examples of coevolutionary genetics, such as plasmids and phage, especially in the writings of Bruce Levin and his colleagues Rich Lenski and Lin Chao. Genomic conflict and many aspects of microbial conflict clearly had close conceptual associations with the evolutionary origins of genomes, cells, and evolutionary units.
Around that time, in the late 1980s, another exciting research trend was developing on host-parasite dynamics. Anderson and May started what quickly became a large new field of study. The initial work primarily focused on ecological dynamics and epidemiology. In my work, I emphasized the genetics of host resistance and parasite host range. My genetic work incorporated ecological dynamics and emphasized demographic aspects of natural selection.
In the early 1990s, I devoted most of my effort to the study of host-parasite genetics. At that time, I thought I would never again do significant new work in social evolution. However, my coevolution interests brought me back to social evolution in a surprising way.
Anderson and May wrote some articles in which they emphasized the problem of parasite virulence. Why do some parasites cause so much harm to their hosts, whereas other parasites cause little damage? Anderson and May noted a key tradeoff between transmission and virulence. If traits that increase parasite transmission necessarily increase virulence, then natural selection may adjust virulence along that tradeoff in response to various demographic and epidemiological factors. Similarly, clearance may trade off with virulence, such that a parasite that increasingly avoids host immune clearance may cause more damage to the host. One can think of transmission rate as parasite birth rate, clearance as parasite death rate, and virulence as also increasing parasite death rate via the damage caused to the host, the parasite’s resource for growth.
Because I was fully into the host-parasite research world at that time, I started to think about virulence. In essence, virulence is just a classic evolutionary life history problem of tradeoff between fecundity and survival. Anderson and May roughly had that life history type of approach. But no one really took the analysis down to the essential level of a pure life history problem, which could be analyzed by the powerful theoretical tools of reproductive value and demography.
In addition, virulence also has a potentially strong aspect of social evolution. One can think of parasites within a host as a collection of individuals competing for a common resource. Often, the parasites within a host derive from one or a few ancestors that invaded the host or from a small number of clones that have come to dominate in the host. In other words, the parasites are often genetic relatives, with varying degrees of clonality and genetic mixing. A few earlier authors noted the group selection or social aspect of virulence, such as Lewontin and Hamilton. But their prior comments were brief.
All of that interest in parasites and virulence refocused my attention on the problems of social evolution, microbial evolution, and the open problems of kin selection and other social processes. While I continued to focus most of my attention on genetic polymorphisms of host-parasite interactions, I began what I thought of as an amusing diversion on studying the problems of sociality among a group of simple replicators. The idea was that parasite virulence essentially ties to the earlier problems of conflict and cooperation over resources among members of a group. How can a more cohesive and essentially unitary group evolve when there is genetic mixing?
I decided to make the problem as simple as possible. I would not worry about how complex sociality might evolve in social insects, in the cooperation among the trillions of cells of complex multicellular organisms, or in the evolution of human sociality as group size increased. Instead, I would think about the essential processes of natural selection on group cohesion when a group of very simple lower level units compete for a local fixed resource. If I could not solve the problem in that very simple case, then I certainly would not make any progress for the more complex problems.
My first article was in the Proceedings of the Royal Society B 1994, in which I analyzed the role of kin selection alone in groups of replicators. Each group, called a protocell, is founded by a random sample of replicators from its parent. A certain mutation rate occurs when a replicator copies itself. The random sampling at founding increases relatedness, and the mutation decreases relatedness.
That article presented what is perhaps the simplest model for the evolution of cooperation and group cohesion. An individual has a trait, z that determines how strongly it competes against its neighbors for access to local resources. The more that individual invests in competition against neighbors, the less efficiently they transform resources into reproduction. Thus, we may write the group productivity as proportional to 1-Z, where Z is the average competitiveness of a group member. The fraction of the total group productivity achieved by an individual is proportional to z/Z, its competitiveness, z, divided by the average competitiveness of group members, Z. The fitness of an individual is therefore w= (z/Z) (1-Z).
In my earlier work on sex allocation, I had developed a very simple optimization method for finding the outcome of natural selection. Take the derivative of fitness with respect to the individual trait value, dw/dz, set the derivative to zero, and solve for the optimum, z*. In this case, the solution is z*=1-r, in which r is the coefficient of relatedness. Here, r is dZ/dz, the derivative of the group competitiveness with respect to individual trait value. I had never published that simple method, instead using a more complex Price equation method in my publications. I began to think that I should publish the method, because it is so useful.
Here, I had an elegantly simple way of expressing the fundamental problem of group cohesion as a function of kin selection theory. As relatedness declines, group cohesion declines. Social unity cannot evolve unless the kin selection coefficient is very high or some other process can overcome the inherent competitiveness of unrelated individuals.
This simple model also expresses the problem of virulence, which is essentially the exploitation and damage to the host arising from parasite exploitation of host resources. As a parasite increasingly exploits the host, it may gain a competitive advantage against neighboring parasites, but its overall fitness may decline because of damage to the host.
The model is also an exact match to the classic sex allocation theory of local mate competition. In that sex allocation model, males compete against neighboring males. The more a mother invests in competitive sons, the fewer productive daughters she makes, and so competitiveness trades off against productivity.
I now had a model showing, in the simplest way, how kin selection determines group cohesion, and how competitiveness inherently erodes group cohesion. In my Nature article, N95, I emphasized this basic model as the essential notion of the tragedy of the commons, also emphasized in my Quarterly Review of Biology article on virulence in 1996. Egbert Leigh had used the phrase “the tragedy of the commons” in an earlier article, taken from Hardin’s 1968 work. However, there were essentially no citations to Hardin or the tragedy of the commons in the evolutionary literature until these very simple models appeared in my articles. Following that, the concept of the tragedy of the commons spread rapidly, perhaps the widest and most enduring contribution of my work in these articles.
That simple model for the tragedy of the commons set my challenge. How can group cohesion and higher level units evolve when the kin selection coefficient is significantly less than one? In other words, how can the tragedy of the commons be overcome when kin selection is not sufficient?
In N95, I developed a solution. When relatedness is high, self restraint evolves and is sufficient. As relatedness declines, individuals are favored to repress the competitiveness of neighbors, thereby preventing the erosion of local productivity and the tragedy of the commons.
The model has two traits, the competitiveness of an individual against neighbors, and the investment by an individual in repressing competition within the group. An individual can invest significantly in competing and simultaneously invest significantly in producing an environment in which competition is repressed. This was the first and still the simplest mathematical model that showed how unity can evolve in spite of limited genetic relatedness.
The mathematical analysis for the joint evolution of two traits in a social interaction can be very complex. I was able to make an approximate analysis by using my optimization method, which I still had not published. The value of the new work motivated me to write to Peter Taylor and try to work out the details of the optimization approach, which we published as How to Make a Kin Selection Model in 1996 in the Journal of Theoretical Biology. All of that got me started again on the theory of social evolution, a topic which I thought I had given up in 1987. After a bit more effort on the details, the new work led to my 1998 book Foundations of Social Evolution.
The tragedy of the commons model and my interest in virulence and microbes led me to write my 1996 Quarterly Review of Biology article on virulence. That article unified the life history and social evolution perspectives applied to microbial traits. Although the article was primarily about virulence, in my mind I saw the foundation for a much richer conceptual and empirical field of microbial evolution, unified with the problems of conflict, cooperation, and evolutionary units at different levels of organization. The final sentence of the abstract of that article is: “The last part of the article connects standard models of parasite virulence to diverse topics, such as the virulence of bacterial plasmids, the evolution of genomes, and the processes that influenced conflict and cooperation among the earliest replicators near the origin of life.” The field of microbial sociality has developed significantly in the past few years. I like to think of that developing field as the natural extension of the fun side projects that I began long ago on social evolution among simple replicators.
The literature on social evolution can be very difficult to read. Authors sometimes assert that their ideas conflict with prevailing concepts when, in fact, there is much less controversy through the history of the subject than first appears. For example, the recent controversial series of articles by Nowak, Tarnita and Wilson emphasized that kin selection theory is not a sufficient explanation for many cases of complex sociality. They presented that conclusion as a novel perspective that contradicted the prevailing view. However, in the paragraphs above, I pointed out that the limitations of kin selection theory formed the widely recognized challenge of social evolution theory in the 1980s. That open challenge eventually led to my N95 article and to many of the key topics in Maynard Smith and Szathmary’s classic 1995 book on the Major Transitions in Evolution.
For those reasons, I suggest that new readers focus on the essential underlying problem, where that problem came from, and how the article attempts to address that problem.
With regard to subsequent literature, I published two follow up articles. In 2003 in Evolution, my article Repression of Competition and the Evolution of Cooperation sets the historical context, reviews the theory, and provides some updates with regard to potential empirical studies. In a 2013 edited volume in honor of Richard Alexander, my article A New Theory of Cooperation provides the simplest introduction to the problem and its history, which might be a good article to read first.
After 2003, the subject continued to develop, with many new articles. I have not followed the literature since that time. I would be interested to hear what others think are the most interesting developments on this topic over the past 15 years.