A regression line across primate genera became a management rule
The number is repeated so often that it has stopped sounding like a finding. W. L. Gore and Associates, the maker of Gore-Tex, is widely reported to have capped individual plant headcounts at around 150 employees, building a new facility rather than letting one grow past it once parking and hallway familiarity started to break down [11]. The same figure is invoked for the size of a well-run company in an infantry battalion, part of a tradition of unit sizing that popular accounts trace back through professional armies since at least the sixteenth century and, more loosely, to Roman antiquity [11]. In 2007 Sweden’s national tax agency reportedly built a reorganization plan around a maximum of 150 employees per office [11]. None of this is controlled evidence; it is applied folklore, adopted by people who found the number convenient and then repeated by people who found the story convenient. The one place the 150-ish range has actually been tested against hard behavioral data at scale is more interesting and less anecdotal: Gonçalves, Perra and Vespignani mined 1.7 million Twitter users’ full conversational histories across six months — 380 million tweets, 25 million extracted conversations — and found that regardless of how many accounts a user followed, the number of people with whom they sustained a stable, reciprocal exchange topped out in a band of roughly 100 to 200 [6]. That is a genuine, independent, quantitative replication of a prediction, run on a medium invented decades after the prediction was made. It is also the exception. Most of what people mean when they invoke “Dunbar’s number” is closer to the Gore-Tex story: a number doing cultural work, not a number being tested.
The prediction itself has a precise origin and it is much narrower than its reputation. Robin Dunbar’s 1992 paper in the Journal of Human Evolution ran a comparative regression across primate genera and found that group size tracked one variable with real predictive power — the ratio of neocortex volume to the volume of the rest of the brain — while the ecological variables he tested alongside it, tied to diet and ranging behavior, did not [1]. Stated as a model, the claim was this:
Group size as a function of relative neocortex volume, nothing else in the model earning its keep. Dunbar’s interpretation was mechanistic rather than merely statistical: neocortical processing capacity limits how many relationships an individual can track simultaneously, groups that exceed the limit fragment, and large stable groups in nature are typically built by welding together smaller grooming cliques rather than by everyone bonding with everyone [1]. A year later, in Behavioral and Brain Sciences, Dunbar ran the human neocortex ratio through the same regression and extrapolated that people should live in stable social groups of roughly 150, a figure he supported by pointing to census data collected from a range of tribal and traditional societies in which groups of about that size recurred as a structural unit [2, 4]. That 1993 paper is doing more work in the popular imagination than any single subsequent study, because it is the paper that actually says “150” about humans. Everything since has either supported it, refined it, or tried to take it apart.
What almost never survives the retelling is how the extrapolation was built: one regression line, fitted to a dataset of the primate genera available to comparative biology in the early 1990s, extended three orders of magnitude past the group sizes actually observed in the data — chimpanzee communities and baboon troops run to the dozens, not the hundreds — to predict a value for a single species that was not, and could not have been, part of the original regression at all. That is not a criticism by itself; extrapolation from a fitted biological relationship is a normal and often productive move, and Dunbar was explicit that he was doing it. But it means the number 150 was never an observation. It was, from the moment it existed, a projection whose reliability depends entirely on whether the underlying regression is the right one to project — a question that would not seriously reopen for almost thirty years.
There is also a distinction worth holding onto through everything that follows: a descriptive claim and a prescriptive one look identical once a number is in circulation, but they are not the same claim. Dunbar’s 1993 paper describes what he predicts human group size tends toward, given a cognitive constraint he believes is real. An organization that redesigns its buildings around a headcount of 150 is doing something else — treating a description of a tendency as a design specification, the way a company might mistake the average height of its employees for a load-bearing constraint on doorway height. The gap between those two uses is exactly where folklore like the Gore-Tex story lives, and it is a gap that exists whether or not the underlying number turns out to be well estimated.
The neocortex could not afford the grooming a hundred and fifty would cost
Dunbar’s 1998 paper in Evolutionary Anthropology generalized the 1992 finding into what is now called the social brain hypothesis: primates have unusually large brains relative to body size compared to other vertebrates, and the reason is social rather than ecological — the cognitive demands of living in a stable, individually-recognized group, tracking who is allied with whom, who owes whom a favor, and who is likely to retaliate for what, select for expanded neural machinery in a way that foraging or predator-avoidance problems do not [3]. This reframed brain evolution as a response to a social environment made of other minds rather than a physical environment made of food and threats, and it explicitly challenged the ecological-intelligence models that had dominated the field before it [3].
The hypothesis needed a bonding mechanism, because tracking relationships is not the same activity as maintaining them, and in nonhuman primates the maintenance mechanism is well documented: social grooming, which is time-expensive, one-to-one, and scales with group size — larger primate groups spend more of the day grooming, not less [4]. Run that relationship forward to a hypothetical group of 150 humans and the arithmetic breaks: the fraction of the waking day that would have to be spent grooming, one relationship at a time, to hold a group that size together becomes implausible for a species that also has to forage, travel and reproduce. Dunbar’s 1993 paper treats this as the actual selection pressure behind language: a bonding technology that lets one signaler service several listeners simultaneously — vocal grooming at a distance, and to more than one target at once — is a way of buying the cohesion benefits of physical grooming without paying grooming’s linear time cost per relationship [2]. In support of this, the same paper reports that in ordinary human conversation, roughly 60 percent of speaking time is spent on gossip in the broad sense: talk about relationships, third parties and personal experience, rather than about the physical world [2]. If that figure is taken at face value, most of what people talk about most of the time is exactly the social-bookkeeping content the hypothesis predicts language evolved to carry.
The mechanism Dunbar proposes for how large groups hold together at all, rather than fragmenting into whatever a single grooming budget can service, is that they are built out of smaller units rather than uniform webs: primate groups above a certain size are not flat networks of equally strong ties but clusters of tight grooming cliques loosely bonded to one another, so that the cognitive load any one individual carries is the load of servicing their own clique plus a thinner set of connections to other cliques, not the load of servicing the whole group at equal intensity [1]. This is also why the hypothesis is a claim about actively maintained relationships rather than about recognition. Dunbar’s ceiling was never meant to describe how many faces a person can identify or how many names they can recall — a much larger and less interesting number — but how many relationships a person can keep in a state requiring regular emotional investment and updating, the kind that would decay into mere acquaintance without upkeep.
This is the theory’s strongest and most falsifiable claim, and it is worth separating cleanly from the number 150 itself, because the two can be true or false independently of each other. It is entirely possible that cognitive constraints on relationship tracking are real, that grooming and language occupy the same functional niche, and that language evolved partly under social selection pressure — while the specific claim that the resulting ceiling sits at 150 rather than 60 or 300 turns out to be an artifact of one regression fitted to one dataset with one set of statistical assumptions. The mechanism and the magnitude are different claims, resting on different evidence, and the dispute that follows is almost entirely about the magnitude.
The evidence fits a layered structure, not a single ceiling
The most-cited empirical support for a human number near 150 comes from Hill and Dunbar’s 2003 study in Human Nature, built around an unusually clean natural behavior: the exchange of Christmas cards, the one occasion in contemporary Western social life when people deliberately contact everyone whose relationship they currently value. Distributing a lengthy, detailed questionnaire through a small number of personal contacts to improve completion rates, the study found that maximum network size — everyone included on a household’s card list — averaged 153.5 individuals, while the mean size of the subset of relationships an individual actively initiated contact with, rather than merely reciprocated, was 124.9 [4]. Both numbers sit close to the 150 that the neocortex regression had predicted a decade earlier. The paper also reports that the proportion of kin within a person’s network stays remarkably stable at around 21 percent regardless of total network size or the person’s age or household type, and that contact frequency within the network is driven by two separable classes of variable — passive constraints like geographic distance and whether someone is a co-worker or living overseas, and active choices like emotional closeness and genetic relatedness [4]. The authors are candid about the design’s limits: it is a convenience sample of Christmas-card-sending households in one cultural context, gathered through personal distributors rather than random sampling, which inflates response rates at some cost to representativeness [4]. It is suggestive ethnographic support, not a controlled replication of the primate regression, and it has never claimed to be more than that.
A more structurally interesting line of evidence treats 150 as one rung on a ladder rather than a standalone ceiling. Zhou, Sornette, Hill and Dunbar applied fractal and discrete-scale-invariance analysis to several independent human social datasets and found, with high statistical confidence, that group sizes cluster into discrete layers related by a roughly constant scaling ratio, rather than spreading continuously across all possible sizes [5]. The layers they identify run: a support clique of about 3 to 5 people; a sympathy group with a mean of 14.3, ranging from 12 to 20; a band with a mean of 42.6, ranging from 30 to 50; a community or cognitive group with a mean of 132.5, close to 150; a megaband with a mean of 566.6, close to 500; and a tribe with a mean of 1,728, ranging from 1,000 to 2,000 [5]. The mean scaling ratio between adjacent layers across their datasets is about 3.52, close enough to the geometric progression 3, 9, 27 that the authors describe the series as approximating powers of three [5]. Read this way, 150 was never claimed to be the unique output of human social cognition; it is the fourth term in a series that also includes a small handful of intimates and a loosely bounded tribe, and the more defensible empirical claim is the discreteness and the ratio between layers, not any single layer’s absolute value. The Twitter finding of a 100-to-200 stable-relationship band sits inside this same layer, and reads less as independent confirmation of “150” specifically than as another dataset landing inside the same wide community-sized rung [6].
It is worth noticing how much rounding happens between this table of measured means and the tidy 5-15-50-150-500-1500 sequence that circulates in popular accounts of Dunbar’s work. The actual reported figures are 3 to 5, a mean of 14.3, a mean of 42.6, a mean of 132.5, a mean of 566.6 and a mean of 1,728 [5] — a real geometric structure, but one with real variance around each rung, not six fixed constants. The popular version smooths that variance away in the same motion that turns “a regression-derived estimate with a stated uncertainty” into “a discovered law.” Both compressions make the finding easier to repeat and slightly less accurate every time it is repeated.
What none of this evidence does — and this matters for what comes next — is re-run Dunbar’s original comparative regression on an updated primate dataset with modern statistical tools. The Christmas-card study and the layered-circle papers are independent lines of human network evidence consistent with a number in the 150 neighborhood; they are not replications of the 1992 method that produced the neighborhood in the first place. By 2021, nobody had gone back to the actual regression — group size against neocortex ratio, across primate genera — with the comparative methods that had become standard in evolutionary biology since 1992. When that finally happened, it did not confirm the number. It took the regression apart.
A 2021 re-analysis returned a confidence interval of two to five hundred and twenty
Patrik Lindenfors, Andreas Wartel and Johan Lind’s 2021 paper in Biology Letters, titled bluntly “‘Dunbar’s number’ deconstructed,” is the direct re-run Dunbar’s original method had never received [7]. The statistical landscape had moved on since 1992 in one specific, technically important way: modern phylogenetic comparative methods treat closely related species as non-independent data points, because two primate genera that share a recent common ancestor are likely to resemble each other on any trait — including neocortex ratio and group size — for reasons that have nothing to do with a causal relationship between the two. Ignoring that shared ancestry inflates the apparent statistical confidence of a cross-species regression. Lindenfors and colleagues applied two families of phylogenetically corrected models — Bayesian multilevel models incorporating a phylogenetic covariance matrix, and phylogenetic generalized least squares regressions — to updated primate brain and group-size data [7]. The general concern these methods are built to address is straightforward once stated: two primate genera that share a recent common ancestor tend to resemble each other on almost any measured trait, neocortex ratio and group size included, simply because they inherited much of their biology from the same source, not because one trait is causally driving the other in either lineage. Treating each genus as an independent data point, the way an uncorrected regression does, effectively double-counts evidence that is shared through descent rather than earned independently — which tends to make a fitted relationship look more precise, and its extrapolations look more trustworthy, than the underlying evidence actually supports.
The headline result is that the choice of method alone moves the point estimate by a factor of several: the phylogenetic generalized least squares models produced point estimates for human group size ranging from 16.4 to 42.0, while the Bayesian multilevel models produced point estimates ranging from 69.2 to 108.6 [7]. Neither range contains 150. But the point estimates are almost beside the point next to the uncertainty around them: the reported 95 percent confidence intervals were 2.1 to 127.7 and 5.2 to 336.3 for the two phylogenetic least-squares specifications, and 3.8 to 520.0 and 4.6 to 520.0 for the two Bayesian specifications [7]. Taking the widest interval at face value, a value anywhere from two people to five hundred and twenty people is statistically consistent with the same data and method family that once yielded a clean 150. The authors’ own conclusion is correspondingly blunt: they write that specifying any one number for human group size from this kind of analysis is futile, and that a cognitive limit on human group size cannot be derived from the primate neocortex-to-group-size relationship using currently available comparative data and methods [7].
It is worth being precise about what this critique does and does not claim. It does not argue that primate group size and relative brain structure are unrelated, and it does not argue that no cognitive constraint on human relationship maintenance exists — the Hill and Dunbar network data and the Zhou et al. layered structure are untouched by it, because neither depends on the 1992 cross-species regression. What it argues, specifically and narrowly, is that the regression Dunbar used to generate 150 does not have the statistical power, once fitted with methods that correctly account for shared ancestry, to license any single number with the confidence popular usage has assigned to it. That is a claim about estimation, not about biology, and it is the kind of claim a field is supposed to be able to settle by checking the math. It did not settle it.
Dunbar and Shultz say the fight is about method, not about humans
Dunbar did not accept the deconstruction as final, and the response, co-authored with Susanne Shultz and published in Biological Reviews in 2023 under the title “Four errors and a fallacy: pitfalls for the unwary in comparative brain analyses,” does not defend the number 150 directly so much as attack the class of statistical reasoning that produced Lindenfors and colleagues’ wide intervals [8]. The paper opens from a broader observation: comparative analysis is the backbone of evolutionary inference, but its track record for producing consensus, especially on what drives large-brain evolution, has been poor, with the field “embroiled in an increasingly polarised debate over the past three decades” [8]. Dunbar and Shultz’s diagnosis is that most of that polarization comes not from irreducible uncertainty in the data but from four recurring classes of conceptual error, compounded by a further logical fallacy: failing to keep Niko Tinbergen’s four levels of biological explanation — mechanism, development, function and evolutionary history — properly separated when testing a hypothesis; misapplying the principle that biological traits only make sense in light of evolution in a way that smuggles in unearned conclusions about adaptation; choosing behavioral proxies that do not actually measure the construct a hypothesis is about; and applying statistical methods that are inappropriate to the structure of the data [8]. Their prescription is a more careful, systems-based approach to comparative hypothesis-testing and a preference for broader rather than narrower taxonomic sampling [8].
The two named frameworks are worth unpacking briefly, because the paper leans on both as diagnostic tools rather than as decoration. Tinbergen’s four questions are a long-standing organizing scheme in behavioral biology distinguishing the immediate physiological mechanism behind a trait, its developmental origin in the individual, its current adaptive function, and its evolutionary history across a lineage — four genuinely different questions that a single correlation, such as one between neocortex ratio and group size, cannot by itself answer all at once. Dobzhansky’s dictum is the much-quoted principle that nothing in biology makes sense except in the light of evolution; Dunbar and Shultz’s complaint is that the dictum gets misapplied when a correlation is treated as automatic proof of adaptive function, skipping the harder work of showing the trait was actually shaped by the selection pressure being proposed rather than by some other route entirely [8]. Applied to the dispute at hand, the implication is that a wide confidence interval is not necessarily evidence that no cognitive limit exists; it may instead be evidence that group size, taken alone, is too blunt a behavioral proxy for whatever the neocortex is actually being selected to do. The paper’s own framing situates it explicitly as a response to exactly the kind of statistical reanalysis Lindenfors and colleagues published two years earlier, arguing that wide confidence intervals can be as much a symptom of a poorly specified model or an ill-chosen proxy as of a genuinely indeterminate biological relationship.
This is not a new fight confined to Dunbar’s number. Alex DeCasien, Scott Williams and James Higham had already unsettled the social brain hypothesis more broadly in a 2017 Nature Ecology & Evolution paper that assembled data on more than 140 primate species — over three times the sample used in earlier comparative work — and updated phylogenies, then found that after controlling for body size and shared ancestry, diet predicted brain size while several standard measures of sociality did not: frugivorous species, and species combining fruit and leaf eating, had larger brains than strict leaf-eaters, a pattern the authors attribute to the cognitive demands of locating and extracting patchy, seasonal fruit resources rather than to the demands of group living [9]. That result directly challenged the premise that social complexity is the primary driver of primate brain expansion, independent of anything to do with humans or the number 150.
The next move in that argument shows what “the wrong statistical method” can actually mean in practice. Mark Grabowski, Bjørn Kopperud, Masahito Tsuboi and Thomas Hansen revisited the diet-versus-sociality dispute in 2022 and argued that the standard phylogenetic generalized least squares approach DeCasien and colleagues used rests on a Brownian-motion model of trait evolution that is not well suited to testing adaptation to an external factor at all [10]. Substituting Ornstein-Uhlenbeck models, which allow a trait to be pulled toward different optima under selection rather than simply drifting, they found that both diet and sociality mattered: more folivorous diets were associated with smaller brains, plausibly because the digestive costs of processing leaves redirect energy away from neural tissue, while more complex social systems were independently associated with larger ones [10]. Neither DeCasien’s finding nor Grabowski’s correction is about Dunbar’s number specifically. Together they show that comparative primate brain-size research has spent the better part of a decade re-litigating which statistical model of trait evolution is the right one to fit before any substantive conclusion — about diet, about sociality, or about a group-size ceiling — can be trusted. The Lindenfors-versus-Dunbar exchange is a specific instance of a field-wide argument, not an isolated dispute about one anthropologist’s favorite number.
What survives the audit, and what does not
Laid side by side, the two camps agree on more than the headlines suggest. Neither side disputes that some relationship exists between measures of primate brain structure and measures of social organization; Lindenfors, Wartel and Lind’s complaint is about the precision claimed for one specific extrapolation, not about whether comparative neuroanatomy has anything to say about sociality at all [7]. Neither side disputes that human beings have layered, differentially-maintained social networks; the Zhou et al. discrete hierarchy and the Hill and Dunbar network data do not depend on the 1992 cross-species regression and are untouched by its statistical troubles [5, 4]. And neither side has produced a replication, in the strict sense, of Dunbar’s original method on an independent dataset that confirms a narrow point estimate near 150; the honest state of the literature is that the one team to attempt a modern re-run of that specific method got confidence intervals wide enough to be nearly uninformative, and the original author’s response, while serious and methodologically substantive, argues for redoing the analysis differently rather than reproducing the original number by other means [7, 8].
It is worth being exact about what “replication” would even mean here, since the word gets used loosely. A replication of Dunbar’s 1992 finding would be an independent team applying a comparative method the field regards as sound to an independently assembled primate dataset and recovering a similar relationship between neocortex ratio and group size, ideally with a similar extrapolated value for humans. Lindenfors, Wartel and Lind did the first half of that — an independent team, a modern method, updated data — and did not recover a similar value, let alone a similarly narrow one [7]. Dunbar and Shultz’s response disputes whether their method counts as sound, which if accepted would mean the replication attempt itself was flawed rather than that the original finding failed to replicate [8]. Until a third party runs the analysis with a method both sides would accept as appropriate, the honest label for the current state of the evidence is not “replicated,” not “refuted,” but “actively contested on methodological grounds that neither side has conceded” — a less satisfying sentence than either camp’s public statements, and a more accurate one.
What does not survive is the version of the claim that circulates furthest from the original papers: that 150 is a precisely derived, universal cognitive ceiling on human relationships, established with the kind of statistical confidence that would let an organization plan around it the way an engineer plans around a material’s known tensile strength. That version was never supported by the 1992 regression as closely examined, and it is actively contradicted by the one attempt to check the regression’s own statistical foundations with contemporary tools [7]. What plausibly does survive is a narrower, less quotable pair of claims: that human social relationships organize into a small number of discrete, nested layers with a roughly consistent scaling ratio between them, a pattern found independently in Christmas-card networks, mobile and online communication data, and fractal analysis of multiple datasets [4, 5, 6]; and that maintaining an active relationship costs cognitive or attentional resources that are finite, which is a claim about mechanism rather than magnitude and survives even if the specific ceiling attached to it does not.
A claim about what would change this reading is worth stating explicitly rather than leaving implicit. If, within the next several years, a re-analysis using an evolutionary model that the field broadly accepts as appropriate — an Ornstein-Uhlenbeck-type model of the kind Grabowski and colleagues applied to the diet-sociality dispute, rather than the Brownian-motion assumptions underlying both the original 1992 regression and Lindenfors and colleagues’ phylogenetic least-squares specifications — is run on an updated primate neocortex and group-size dataset and returns a confidence interval substantially narrower than an order of magnitude, that would be a genuine vindication of something close to Dunbar’s original approach, even if the resulting point estimate is not exactly 150. The observable indicator is straightforward: a published comparative analysis, using a model class contemporaries treat as statistically appropriate for adaptive hypotheses, reporting a 95 percent interval for human group size tighter than roughly one order of magnitude. The disconfirmation condition is equally clear: if such an analysis, run with methods the field has already converged on as correct, still returns an interval spanning hundreds of individuals, that would confirm Lindenfors and colleagues’ position was not an artifact of choosing the wrong statistical family but a real limit on what this kind of cross-species extrapolation can tell us about one species sitting at the extreme edge of the data.
The specimen is the self-audit
What makes this dispute worth following is not, in the end, whether the true number is 150, or 108, or somewhere in a band nobody has pinned down yet. It is that a widely popularized finding got checked, thirty years after publication, against the field’s own improved statistical standards, by researchers with no stake in preserving it — and that the checking produced not silence, not a quiet retraction, but a public methodological argument that is still active, generating new comparative papers on questions adjacent to the original one. DeCasien’s diet-versus-sociality challenge and Grabowski’s Ornstein-Uhlenbeck correction were not written about Dunbar’s number at all, and yet they are part of the same audit, because they are testing the same class of comparative claim with the same family of tools whose adequacy is precisely what the Dunbar-Lindenfors exchange turns on. A science that can only produce beloved numbers, and never re-examine them once they have escaped into management books and army field manuals, is not doing its job. A science that re-examines them, argues in public about exactly where the original method went wrong or didn’t, and leaves a paper trail specific enough for the next generation of comparative biologists to check again, is doing exactly what it should. The number that might not exist is, in that sense, less interesting than the fact that anyone went back to look.
