EDGE 47

(11,159 words)

John Brockman, Editor and Publisher | Kip Parent, Webmaster

THE THIRD CULTURE

[Editor's Note: See "How Is Personality Formed?" A Talk with Frank J. Sulloway in EDGE 40 — and also the response by Judith Rich Harris in EDGE 42 ).

FRANK SULLOWAY RESPONDS TO JUDITH RICH HARRIS

Birth Order and The Nurture Misassumption: A Reply to Judith Harris

INTRODUCTION

It is odd to find myself being criticized by Judith Harris in her commentary on my EDGE interview with John Brockman. This is because we share so much in common in our views about the origins of personality. For example, we agree that parents have relatively little direct impact on the personalities of their children. We also agree that genetics accounts for a substantial source of personality differences among human beings.

Where Harris and I disagree is over the nature of the specific environmental influences that are important in personality development. Harris ascribes these environmental sources almost entirely to the peer group--that is, to influences operating outside of the family environment. In particular, she contends in her book The Nurture Assumption that the influence of parents ends with conception. By contrast, I believe that a variety of influences, both inside and outside of the family, contribute to individual differences in personality. In this connection, I certainly support Harris's thesis that peer groups affect personality, and I applaud her constructive arguments on this topic. However, I also believe that Harris has pushed her thesis much too far, and that her rather extreme stand on this subject has led her to deny solid evidence in favor of within-family influences.

Much of the relevant evidence on within-family influences was presented in my recent book Born to Rebel: Birth Order, Family Dynamics, and Creative Lives. Based on 26 years of research involving 6,566 participants in 121 radical revolutions and reform movements, I demonstrated that birth order and other aspects of family niches are systematically related to personality for a variety of different traits. Furthermore, these behavioral findings hold when the data are controlled for sibship size, social class, and various other background influences that have tended to confound the results of previous studies on this subject.

BIRTH-ORDER RESEARCH: JUDITH HARRIS'S ACHILLES HEEL

The critical relevance of birth-order research to Harris's controversial thesis about the family is best understood in connection with the cumulative findings of behavioral geneticists. In studies of twins raised together and apart, researchers have shown that about 40 percent of the variance in personality traits is attributable to genetics. Another 35 percent of the variance is attributable to the nonshared environment (that is, experiences that are not shared by siblings who have grown up together). Of the remaining variance in personality, about 20 percent is associated with errors in measurement, which leaves just 5 percent that can be explained by the shared environment (or family milieu).

One of the most important unanswered questions arising from these behavioral genetics findings is the precise nature of the nonshared environment, which constitutes the lion's share of all environmental influences. The nonshared environment has two main sources: family microenvironments and those extrafamilial experiences, including peer group influences, that are not shared by siblings. By proclaiming that personality is primarily shaped by peer groups, Harris is forced to deny an overwhelming body of evidence that supports the influence of family microenvironments on personality. The single most convincing threat to Harris's extreme thesis is the voluminous research on birth order. Because there are no genes for being a firstborn or a laterborn, birth-order effects must be attributed to differences in within-family environments. (1)

At first glance, the literature on birth order does not appear to provide encouraging support for the influence of family microenvironments. In their important 1983 book, two Swiss investigators--Cecile Ernst and Jules Angst--undertook a comprehensive review of more than a thousand studies on this subject that had appeared between 1946 and 1980. Ernst and Angst argued that when studies are controlled for background factors that often confound results (and lead to spurious conclusions), birth-order differences are not generally observed. They concluded that birth-order effects are mostly artifacts of uncontrolled background influences, principally differences in social class and sibship size.

Based on Ernst and Angst's critical verdict, Harris reiterated this viewpoint in her 1995 Psychological Review article that outlined the basic thesis of her new book. Unfortunately, Ernst and Angst's literature review was impressionistic--that is, conducted without the benefit meta-analytic techniques, which, in the early 1980s, were beginning to be employed in the biomedical and social sciences. In the Preface to their 1983 book, these two authors regretted that they had not taken advantage of these newer methods, which have shown themselves, in the interim, to be far more reliable than impressionistic forms of review.

In an article published in 1995, I performed what is called a "vote counting" meta-analysis of the birth-order data summarized in Ernst and Angst's book. In this form of meta-analysis, the number of significant findings in the published literature is compared with the number of null outcomes. For those studies reported as being controlled for social class or sibship size, I found a confirmation rate of 37 percent for 196 controlled findings. To the nonspecialist, such a modest confirmation rate might seem lackluster, but it is actually statistically impressive because the expected hit rate is nowhere near 100 percent. Given the median size of birth-order studies (about 250 subjects) and assuming that birth-order effects on personality are roughly of the same magnitude as those observed for age and sex, the best one could possibly hope for is a confirmation rate of about 50-60 percent. By contrast, if there are no true birth-order effects, the expected confirmation rate is only 2.5 percent (based on a two-tailed statistical test). Thus, the observed confirmation rate for birth order effects is 15 times higher than the expected rate and leads to a very different conclusion than Ernst and Angst themselves reached. These impressive meta-analytic findings represent the Achilles heel of Harris's argument about personality development, which explains why Harris is so concerned about repudiating these findings.

META-ANALYTIC MADNESS

In my 1996 book Born to Rebel, I summarized my previous meta-analytic results in the context of a Darwinian theory of personality development based on sibling competition. It is relevant that Harris's own response to my book was inspired by a review in Science magazine, by the historian John Modell, who remarked that he had been unable to replicate my meta-analytic totals. When I contacted Modell in order to find out exactly why he had been unable to replicate my results, it became apparent that Modell had overlooked a crucial footnote at the bottom of the table in which I presented my meta-analytic findings. In this footnote, I explicitly state that I had tallied my results in terms of individual "findings" rather than "studies." Because Modell counted studies--ignoring multiple findings in the same study--he naturally obtained different totals. Modell subsequently acknowledged his mistake to me (personal communication).

Meta-analytic tallies in terms of "studies" make no sense. Findings are what matter. This is especially true given the goals of my own meta-analysis, which sought to test specific hypotheses about sibling strategies in terms of the Big Five personality dimensions. For example, I expected firstborns to be more conscientious than laterborns, and I expected laterborns to be more agreeable and open to experience than firstborns. Each birth-order study may report multiple findings relevant to each of these different hypotheses. A single study may therefore confirm one hypothesis and refute others. In addition, a study with multiple findings should not be given the same weight as a study containing only a single finding. Thus Modell's decision to count studies rather than findings was an inherently bad idea.

Unfortunately, Judith Harris followed in Modell's methodological footsteps, basing her own meta-analytic counts on "studies." She did so in spite of being fully aware that my own counts were by "findings." Additionally, she made no effort to ascertain how these two alternative methods of counting might differ in their outcomes. Harris subsequently submitted her meta-analytic results to two mainstream psychology journals, both of which rejected her manuscripts. As a reviewer for the second of these two journals, I first became aware of the discussion and arguments that are now presented, in much the same form, in Harris's EDGE commentary and as Appendix 1 of her book.

Not only does counting by studies lead to different results (a fact that Harris eagerly exploited as part of her critique), but it also distorts the ratio between confirmations and refutations. If, for example, a given study reported that firstborns are more conscientious than laterborns, but also more agreeable, I counted one confirmation and one refutation (in accordance with my formal hypotheses for these two dimensions). By contrast, Harris classified such "mixed" results as a single null outcome. Harris's method of counting "mixed" results as nulls tends to underestimate the number of confirming findings and to overestimate the number of nulls, skewing the results in favor of her own theoretical biases. By contrast, Harris's equally inappropriate procedure of counting interaction effects as single positive or negative outcomes has the opposite consequence. (An interaction effect occurs, for example, when birth-order effects hold for men but not for women.) It would be nice to think that these two sources of errors cancel one another out, but Harris did not discuss this issue.

There is another reason why Modell and Harris both obtained differing meta-analytic totals from my own: unbeknownst to them, their tallies were riddled with errors. Neither of these two investigators consulted the original literature, relying instead on Ernst and Angst's (1983) summaries of the birth-order research through 1980. It is customary for researchers performing a meta-analysis of a specific literature to actually read the original literature. Accordingly, before I undertook my own meta-analysis, I examined more than two hundred of the original publications in an effort to verify Ernst and Angst's tabulations. In the process, I found at least 45 errors and inconsistencies, which I corrected before tallying my results. (A formal compilation of these errors is available from the author.) Last January, I sent a complete list of these errors to Judith Harris, indicating the publications involved, the specific nature of the reporting errors, and the pages in Ernst and Angst's book where the reporting errors occur. During the seven months between her receipt of this list of errors and the publication of her book, Harris made no attempt to verify these inaccuracies or to implement the necessary corrections in her own tallies. Instead, she has published her original tallies in unaltered form as part of her critique of my own meta-analysis. She has also withheld from her readers the extent of these errors, as well as her own prior knowledge of this information. In science, the knowing publication of erroneous data is considered serious misconduct. (2)

Given Harris's inappropriate method of counting "studies" rather than "findings," as well as her refusal to correct her counts for the 40-odd errors that I identified in her overall tallies, it is hardly surprising that Harris and I reached differing totals in our respective meta analytic counts. In spite of these errors, Harris's confirmation rate was only modestly lower than mine (29 percent, for 179 studies, versus 37 percent for my total of 196 findings). Moreover, her tallies--distorted as they were--did not support her theoretical position, which becomes apparent when statistical tests are applied to her results.

THE FILE DRAWER PROBLEM

A confirmation rate of 29 percent is generally considered impressive by meta-analytic standards. This high a proportion of confirming results would arise by chance considerably less than once in a million times. This strong degree of statistical support creates a problem for Harris's thesis. She has attempted to reconcile this difficulty by claiming that these meta-analytic results cannot be analyzed statistically. (3) Because some studies report more than one finding, Harris notes, multiple findings from the same population are not statistically independent. This assertion is true, but Harris fails to point out that it is true only in a limited sense. About a third of the studies in both of our meta-analytic surveys report only one finding, and the likelihood of these findings arising by chance is also less than one in a million. In other words, the trend toward significant birth-order findings is sufficiently pronounced that it remains even if two-thirds of the data are thrown away.

Harris has raised a second objection to the use of statistical testing. Birth-order researchers, she claims, have employed a "divide-and-conquer" strategy by testing for birth-order effects in subsamples. Because it is not generally known how many of these subsamples may have been tested, Harris maintains that one cannot apply the normal rules of probability to the resulting findings. This claim is a variant of the so-called "file drawer" problem, which involves the tendency for investigators to publish their significant findings but for these same investigators to leave their nonsignificant findings lying around in file drawers. In my 1995 article, as well as in my 1996 book, I discussed this important issue, a point that Harris fails to bring to the attention of her readers (who are thereby encouraged to think that I did not consider it). In this particular context, moreover, Harris's claims about the file drawer problem are misleading. In both Harris's and my own meta-analytic totals, confirming findings involving interaction effects do not occur more often than expected by chance, compared with other kinds of significant findings, whereas the opposite outcome ought to be the case if Harris's speculative assertion has any merit. (4)

By this point, we can perceive a characteristic style to Harris's mode of argument. She begins by casting doubt on the validity of birth-order results, but she invariably fails to test her claims by using readily available data that might either confirm or refute her position. Here is one more example of a formal test that refutes Harris's own claims and findings. Let us grant, as most researchers do, that file drawers contain a higher proportion of null findings than does the published literature. This tendency would presumably not affect the publication of significant findings that refute other researcher's claims about birth order. In my own meta-analysis, the number of significant confirming findings exceeds the number of significant refuting findings by a 5-to-1 ratio, which would occur by chance less than once in a million times (and less than once in ten thousand times if we throw away two thirds of the data by ignoring all studies reporting more than one finding). For Harris's own totals, the ratio of confirming to negating findings is 4 to 1, which would occur by chance less than once in a hundred thousand times (and less than once in a thousand times if we again choose to ignore studies reporting more than one finding). In short, it is not only possible, but appropriate, to apply statistical tests to these birth-order results. For obvious reasons, Harris would rather not do so.

SELF-REPORT DATA VERSUS REAL-LIFE DATA

In Born to Rebel I noted that real-life studies--those based on observable behavior--yield a significantly higher proportion of confirming studies than do self-report personality measures. (5) Radical revolutions in history provide a dramatic case in point, which leads Harris to engage in what appears to be another misrepresentation. For example, she claims that my assessment of attitudes toward revolutionary change in history involved only "a single question," remarking: "How well can we judge someone's personality by his answer to a single question?" In actual fact, my historical survey of 6,556 individuals involved responses to more than a hundred different historical events. None of these events involved a single question. Consider the case of Darwinism, which — at minimum--required Darwin's contemporaries to make judgments about organic evolution in general, the evolution of mankind, and Darwin's own controversial theory of natural selection. The number of questions that I and my 110 expert raters assessed in this historical study varied by event. For example, my analysis of attitudes toward the Reign of Terror among the 893 deputies of the French National Convention (1792-94) involved six different votes that took place within the Convention; the decision to sign, or not to sign, a document protesting illegal actions within the Convention; and 19 different measures of political activity, which I combined into an overall scale of tough-mindedness. (6) In assessing openness to experience among the 3,890 scientists who participated in 28 scientific revolutions, I employed five different measures: religious and political attitudes (as rated by 94 expert historians), world travel, breadth of intellectual interests, and openness to radical innovations (as judged by 110 expert historians). (7) In conclusion, it is an outrageous misrepresentation of the facts for Harris to say that the historical data presented in Born to Rebel reflect responses to only "a single question."

Harris places a high degree of reliance on self-report studies, whereas I am more cautious about such measures. Over the last year I have conducted one of the largest birth-order studies ever undertaken in order to determine why self-report data are often less supportive of birth-order effects than are real-life studies. This new study involves more than 5,700 subjects who rated themselves, their siblings, friends, spouses, and, in some cases, their parents and offspring.

One of the most serious problems with self-report data is that measurement scales are typically unanchored. What does it mean for us to assign ourselves a "7" on a 9-step scale for empathy, given that we have no accurate idea about who belongs at the closest reference points (6 and 8)? In a study of 660 CEOs, I found only minimal birth-order effects based on self-ratings using unanchored scales. By contrast, when I had the same CEOs rate themselves relative to a sibling, birth-order effects were highly significant and a whopping 5 times larger than by the previous method of assessment. Using this same method of direct sibling comparisons with more than 4,800 additional subjects, aged 8 to 95, I have confirmed every general claim about personality that I made in Born to Rebel. In terms of their overall magnitude, birth-order effects for 30 different personality traits are somewhat smaller than those for sex but somewhat larger than those for age (Sulloway, in press). (8) Moreover, the similarity between the effect sizes for Big Five personality dimensions in this new study, and the confirmation rates for the same personality dimensions in my previous meta-analysis of the birth-order literature, is reflected by the substantial correlation, which is .89. In other words, meta-analysis provides a remarkably accurate measure of the birth-order trends that are recognized by siblings themselves.

Harris maintains that we leave our birth orders behind us when we depart the family for the wider world, a claim that is fundamental to her peer-based theory of personality development. In order to test this assertion, I asked 757 people to rate themselves and their spouses on 30 personality traits. Not only do ratings among spouses reveal significant birth order differences, but these differences are almost as large as those found in direct sibling comparisons. In addition, the specific traits that exhibit these birth-order differences are the same traits that correlate significantly with birth order in direct sibling comparisons. (9) I have recently replicated this result in a sample of 135 roommates, which demonstrates that unrelated individuals recognize birth-order effects in the people with whom they live on a day-to-day basis. (10) In sum, birth-order effects are not limited to sibling relationships or confined, as Harris argues, to behavior within the family. On this crucial matter, her theory is clearly falsified. The theory is also falsified by evidence relating to other aspects of family niches, including age spacing between siblings and changes in functional birth order owing to the death of siblings or the acquisition of step-siblings.

For some traits, middle children score significantly higher or lower than either firstborns or lastborns. In my previous interview with John Brockman, I cited Catherine Salmon's recent researches bearing on this topic (Salmon 1998; Salmon, in press; and Salmon and Daly, 1998). By testing a series of Darwinian hypotheses about middle children in a variety of different behavioral contexts, Salmon found that middle children, compared with their siblings, are less closely tied to parents and more closely identified with their peers. In her commentary on my interview with John Brockman, Judith Harris ridiculed my discussion of Salmon's study, saying that "the fun part" in birth-order research comes in making up ad hoc explanations to fit such findings. It is worth noting that Harris had not read any of Salmon's studies; this is of a piece with her less than thorough study of the original birth-order literature. (11) To be sure, reading the original literature on any subject does not guarantee the accuracy of one's conclusions. But it is generally thought to help.

CONCLUSION

Birth-order effects are alive and well in the psychological literature, despite Judith Harris's claims to the contrary. Birth-order effects are just the tip of the iceberg in terms of how family environments resolve themselves into a series of microenvironments for each individual member. Apart from the effects of birth order, we know very little about the ways in which the nonshared environment influences human development, mainly because psychologists have not been successful in developing direct measures of this environment. The challenge for future researchers lies in devising ways to test competing hypotheses that bear on the nature and influence of this elusive environment. Peer groups are doubtless an important aspect of this source of environmental influences, but so are family microenvironments, as well as life experiences more generally. To claim, as Harris does, that peer groups explain almost everything about the environmental sources of personality, and that family microenvironments explain almost nothing, seems like a scientific parody of the currently known facts.

CITATIONS AND NOTES — See Below.

FRANK J. SULLOWAY is the author of Freud, Biologist of the Mind : Beyond the Psychoanalytic Legend, and Born to Rebel : Birth Order, Family Dynamics, and Creative Lives. -

THE REALITY CLUB

Philip W. Anderson on John McWhorter's "The Demise of Affirmative Action at Berkeley: Dissecting the Stalemate"

From: Philip W. Anderson
Submitted: 8.26.98
Anyone who has taught blacks even briefly is likely to have encountered the syndrome which McWhorter is talking about. It is good to have it openly discussed and I enjoyed his piece. But I found my quantitative sense somewhat disturbed by the statistics he gave. when one has figures near 50% of single-parent families and 20% young blacks unemployed (admittedly, my memory may predate Clinton prosperity) it is hard to fit these numbers into a 2 1/2% underclass. Not to mention everyone's anecdotal evidence based on his neighborhood problem city, in my case Trenton — and NJ has ten Trentons at least.

It seemed to me that the argument did not need to rest on arguable statistics.

One of the problems with Affirmative Action is that it seems to be perpetuating a racist definition of race. We are all using an antebellum Southern definition of black as — ugh!! — any 'touch of the tarbrush". When I have to fill out the official report of a hiring, no matter in what capacity, i have to classify all of the candidates considered in a truly weird set of categories, especially so because there are a lot of physicists all over Asia, and a lot of Latin American refugee intellectuals who would spit if they knew that they willy-nilly have to be Hispanic whether they speak Portuguese, Italian, or for that matter Nachua. But the worst is that black trumps all other identities — like Tiger Woods. And what is Vijay Singh? — Fijian, for those who don't follow the sports news. In India, incidentally, blacker is often more intellectual.

A possibly irrelevant diatribe, but the point that the problem, insofar as it is one, is cultural, is a good one — it's the culture, stupid!

PHILIP W. ANDERSON is a Nobel laureate physicist at Princeton and one of the leading theorists on superconductivity.

John McWhorter responds to David Bunnell & Daniel C. Dennett

From: John McWhorter
Submitted: 11.13.98
Anyone reading my essay will clearly see that I carefully address the income/class discrepancy in many black families; as it happens, I lived in a whole neighborhood of such families for half of my childhood. I know that scene well — however, the simple existence of such families — which is nothing less than unexpected — does not automatically signify that they are a norm, and in my view there is nothing whatsoever that suggests that they are. I can assure Bunnell that if he had occasion to spend time teaching Berkeley's African American undergraduates, he would be hard put to characterize any but a fraction of them "working class" in any sense of the term.

The very fact that Bunnell is so quick to designate as a norm what is more likely a subsidiary lag is telling. Never have I heard anyone even consider it germane to specify how prevalent this income/class discrepancy might be; instead, the simple fact that such families exist is automatically taken to mean that this is the typical situation. The very sorts of thinking people who decry the public's tendency to conceive of the black fraction of the welfare caseload as its totality have, on the other hand, no problem treating this income/class discrepancy as the lay of the land.

Bunnell's perspective is understandable in its way, demonstrating how difficult it is for us to shake the habit of associating "blackness" with lower-income culture. The problem is that this tendency is now the source of the latest roadblock Affirmative Action fans have begun to throw in the path of constructive engagement with the issue.

My mother worked two jobs at a time (social work professor and child psychologist); my father worked as well (public university administrator). In no sense of the term were we "working class" people; on the contrary, my parents were paradigm examples of the modern middle class family struggling with overextended credit cards and extra jobs to make ends meet. My parents were not atypical among black couples of their generation. Both grew up working class, and were beneficiaries of desegregation, earning their degrees in the 1970s while raising children. Nor, as one might object, were their jobs ritzier than most of today's Berkeley undergrads' parents'. Ask any number of black Berkeley undergrads what their parents do, and you will hear precious few say that their parents drive buses or work part-time at UPS.

Finally, even if in the aggregate one might suppose that black middle class families lean closer to the working class cultural band than whites, this would not suffice as an explanation for the lag in black/white scholarly performance. For example, even low-income Asians score much better than blacks on average on tests and also make higher grades, and yet many of their parents are uneducated and work two jobs at a time, there are few books in their homes, etc.

What, then, makes us so naturally perceive these problems as crippling in black homes as opposed to Asian ones? "Well, Asian culture values scholarly achievement more than black culture" would be almost anyone's answer. Which is precisely my answer. Black students do not lag behind because of working class cultural echoes. They lag behind because of ingrained aspects of the culture which transcend class and reach even into the ritziest households which no one could begin to call "working class" on any level.

Most dismaying, though, is Bunnell's conviction that my opinion should not even be heard. Let us recall: I favor Affirmative Action in the business realm, and would even support it in university admissions if based on class — and yet my essay is a mere "diatribe" written by someone with their "head in the sand". The serene conviction among Affirmative Action advocates that opposing opinions deserve no more of an airing than a speech by Adolf Hitler stems from a sense that all forms of Affirmative Action — except perhaps the most glaringly inefficacious misapplications — are as morally unassailable and celestially anointed as feeding the hungry. Clearly, however, the mounting body of sober objections indicates at the very least that some issues are up for debate.

The insistence among many that they are not — and what is frightening is that I believe that this conviction is genuine, not a mere strategical ploy as Shelby Steele argues in his latest book — is precisely what prevents so many "discussions" of Affirmative Action from being anything but disguised pep rallies for the old status quo. John Hope Franklin's casual rejection of Ward Connerly and the Thernstroms from the "national debate" on race, and members of the African-American National Bar Association's recent attempt to bar Clarence Thomas from speaking before them, are further examples of how on this topic, people who consider themselves more open-minded than those they would designate "conservative" have become as reflexively resistant to even civil dialogue as the Jesse Helmses most of us are so secure in dismissing.

In reference to Daniel Dennett's comment, I have not meant to imply that there is no respect for education in the black community. However, while most African-Americans would certainly praise education on the overt level, there is an underlying ambivalence towards the black "braniac", the sense being that too hearty an embrace of book knowledge tends to draw a person away from identification with "black" concerns. To be fair, it often does — but the fact remains that this ambivalence profoundly affects black students' school performance — most importantly, on all class levels, not just in ghettos.

An illustration: As a graduate student, I once gave a report on the verb "to be" in Swahili. Some months later, a fellow black graduate student told me that the zeal with which I had approached the subject had made them wonder whether I was "a brother" or not. In other words, even for this graduate student in my own department, my commitment to knowledge for knowledge's sake — as opposed to their study of Black English — was suspicious. Yet this type of sentiment is so typical that at the time it barely threw me; it is part of the warp and woof of growing up African-American. Any black kid — on ANY class level — is suckled on this attitude from birth. Only later have I come to reconceive this as having been a demonstration of a grave cultural problem.

This tendency continues even among tenured university professors. When the Oakland school board declared that black children were to be taught standard English via translation from their "native language" Ebonics, when consulted by the media I argued that Oakland was on the wrong track. I brought various data to bear, such as showing that children worldwide learn standard dialects in school without translation when their home dialects are so different from the standard as to be practically a different tongue; that Black English is not in any sense an "African" language; and even that over the years a great many studies have shown that the "Ebonics" method of teaching black children does not work.

Unfortunately, I found myself alone here. The sister currents of victimology and separatism led black linguists and educators to stand behind Oakland's decision almost to a man. Few of my observations were unknown to them, but my choosing to say these things rather than politely skirting over them in favor of a vague "support for addressing the needs of African-American children" was nevertheless considered a breach of racial solidarity. To this day several are distinctly cool in their relations towards me, with the guru of the "Ebonics" approach even having sent me a string of invective-laced hate mail. The crucial thing here was this: barely any of my critics has ever even considered it germane to address my reasoning itself, and never in anything approaching detail. The message is painfully clear — whatever its validity, the primary value of knowledge is its usefulness in The Struggle, to the extent that even distorted knowledge is permissible; otherwise, it is of marginal concern.

Thus few blacks would overtly condemn education, but underlying this formal support is a sense that books for books' sake is essentially for whitey. My Black Musical Theatre history class at Berkeley has been a kind of laboratory test of this. The first time I taught it most of the students were white, the next time, almost all black. I could count on the black students' ears to perk up when I discussed racism and segregation in the industry. However, when it came to things such as what decade (not even year) a musical appeared in or who the principal performer was, whereas most of the white students delighted in this sort of thing as interesting "lore", for most of the black students it was clear that the very same lectures I had given the white students might as well have been pages from the Pittsburgh phone book. A few of them even casually expressed surprise and dismay that I expected them to know such things for the midterm.

I don't mean to sound dismissive of these students; the appearance of such may be part of what arouses Bunnell's response. Although I openly admit that my patience wears thinner with tenured colleagues, on the individual, social level the students tend to be my favorites. However, I at the same time see that they are almost all under the sway of an understandable but pernicious culturally-based holding pattern, whose depth I can only get across with unvarnished descriptions. My main intention is to explore what we can do about this. My ideal would be for this tendency to decrease with the generations to come, rather than increase, as I fear the current sociopolitical climate is ensuring. -

JOHN H. MCWHORTER, Assistant Professor of Linguistics at the University of California at Berkeley, is the author of The Word on the Street.

Catherine Bateson, George Dyson, Douglas Rushkoff, and Duncan Steel on Stewart Brand's "The Clock of the Long Now"

From: Catherine Bateson
Submitted: 8.26.98
Since I first started hearing about the Y2K problem I have been wondering whether it offered an opportunity to get beyond some of the ethnocentricity in our ways of reckoning time. Like Danny Hillis, I had thought of the approximate date of the neolithic revolution 10K years ago as more meaningful, though it is still a local phenomenon and of course cannot be identified with precision. Because knowledge of the past get fuzzy as you go back more than a few thousand years, it makes sense to have a minus calculation. But that leaves us supporting a cosmology in which the (approximate) birthdate of Jesus is the center of everything. Some of that is masked by the convention of referring to dates as C.E. (Common Era) or B.C.E. which is at least an improvement in courtesy. A system beginning 10K years ago would scoop up the Jewish creation date and the Shah's date for the Persian monarchy — but are there other beginning dates in circulation? Check out India and China.

The use of five digits in Danny's system would borrow the specificity and familiarity of the C.E. dating but at least eliminate the notion of that as the beginning of everything.

But...why is this project being double locked into parochialism by location? Surely the actual clock should not be built in either in the US (or in Greenwich) but, say, in 3 different locations on the planet (or maybe 2, to organize around hemispheres — Australia has lots of desert.) Three is a sacred number in many traditions beside the western one, all the integers have a certain sacrality, 2 is surely the sacred number of the computer age!) Disney is greatly interested in becoming more universal, but any imagery that claims to unite the world cannot be centered in the Sonoran desert!

Or perhaps the planning for multiple sites should address climate change as well as urbanization, with more than one scenario taken into account, drastic cooling and drastic warming. Will Epcot be submerged? In a new Ice Age one would not want one's fancy technology to be in the path of a glacier! Archeological time is often vertical.

Think of esperanto — invented as a universal language, it is in fact a composite of European languages. Time to do better.

MARY CATHERINE BATESON is Clarence Robinson Professor of Anthropology and English at George Mason University; author of With a Daughter's Eye; Our Own Metaphor; Angels Fear (written with Gregory Bateson), Composing A Life; Peripheral Visions: Learning Along The Way.

From: George Dyson
Submitted: 8.18.98

When I pick up the morning paper and read that gigahertz processors are slated for the production line, I'm left a bit nervous for the remainder of the day. But I sleep better at night, knowing that Danny Hillis and Stewart Brand are pushing our clock cycles 20 orders of magnitude the other way.

In early 1680, Robert Hooke (physicist, clock-maker, and imagineer, much like Danny Hillis but with a bad temper) introduced the idea of the "Sensible Moment," in his "Hypothetical Explication of Memory; how the Organs made use of by the Mind in its Operation may be Mechanically understood": "And I do not at all doubt but that the sensible Moments of Creatures are somewhat proportion'd to their Bulk, and that the less a Creature is, the shorter are its sensible Moments; and that a Creature that is a hundred times less than a Man, may distinguish a hundred Moments in the time that a Man distinguishes one... So that many of those Creatures that seem to be very short lived in respect to Man, may yet rationally enough be supposed to have lived, and been sensible of and distinguished as many Moments of time(and) as many distinct Differences of Moments, as a Man hath in the Age he lives."

High-speed memory and high-speed processing have produced astonishing results by dividing time into increments of microsecond and now nanosecond scale. Equally important, if less measurable, is the extension of our Sensible Moment, through mechanical intelligence of one form or another, towards the Long Now that Danny's clock epitomizes so well.

GEORGE DYSON is the leading authority in the field of Russian Aleut kayaks, he has been a subject of the PBS television show Scientific American Frontiers. He is the author of Baidarka, and Darwin Among The Machines:The Evolution Of Global Intelligence.

From: Douglas Rushkoff
Submitted: 8.22.98

It wasn't until Stewart described the Clock project to me that I understood what the last thirty or so years of his work was about. From demanding a photo of the earth to publicizing the Pranksters, founding the well or scenario planning — it's less about results and agendas than teaching people to "suppose." The trick is changing perspective, which in most cases seems to mean pulling back, or zooming out.

Oddly, for our obsession-driven culture, learning to go macro — in time, space, communications — is precisely the kind of therapy we need. When a society can spend a year or more avidly deconstructing the minute details of a president's penile activities (I refuse to call what he does sex) it is a fair indication of our ability to hone in. Our shock and confusion about the nature of the terrorist attacks against our embassies and Clinton's military response show just how distracted we have been by the details, and how utterly unprepared we are to consider the big picture (in this case, the symbolic war against US targets who, like cell phone owners, can be tagged and found wherever they might roam regardless of territory.)

And finally, like a Christo wrapping, it's less important whether any of these projects actually happen (though the Grateful Dead *did* finally show up as promised by the Pranksters) than that they be considered. The main reason to implement them is so that the thought experiment can be experienced by those who are not in a position to "get it" by reading The EDGE.

DOUGLAS RUSHKOFF is the author of Cyberia, Media Virus, Children of Chaos, Ecstasy Club and the upcoming Coercion: Why We Listen to What "They" Say.

From: Duncan Steel
Submitted: 8.22.98

Problems for the 10,000 year clock

I liked the concept for the 10,000 year clock, but it's a concept which does not seem realizeable. There are several insurmountable problems if the intention is to let it tick away on its own into the future, unless one accepts gross inaccuracies occurring. Let me give an example. Stewart Brand said:

"Danny wanted to make an instrument that was not participating in those rapid exponential curves of population and technology growth and megabytes per dollar and so on, but something that just plugs along at the same pace as seasons - spring, summer, fall, winter, spring, summer, fall, winter it's the same 10000 years from now probably as 10000 years ago."

Well, no, that last clause is incorrect.

Let me start by asking "What is the pace of the seasons?" At school you've all learnt that the seasons depend mainly on the tilt of the Earth's spin axis, and the time taken to come back to the same orientation is a little less than 365.25 days, and that's the reason for the leap year cycle (leap year every fourth year except in those divisible by 100 but not by 400: AD 2000 is a leap year, but 1800, 1900 were not). This period (a little under 365.25 days) is called the tropical year, and I will not bore you with technicalities on its definition here (although see below). Unfortunately a recent analysis of temperature records stretching back over 300 years (see David Thompson's paper in SCIENCE, April 1995) has shown that the cyclicity/pace of the seasons in the present epoch (over that period from the 17th century to now) is not the tropical year at all, but the anomalistic year (the time between perihelion passages of the Earth), which is actually a little LONGER than 365.25 days. Thus one could claim that instead of LOSING leap year days from 1800 or 1900 or 2100 we actually need to maintain them. Indeed to fit against the anomalistic year one needs every fourth year being a leap year PLUS an additional day every century, which one could accommodate by making every '00 year a super leap year with 367 days (a January Zero to recover?). This would only be a temporary need, however, I would anticipate: I would interpret Thompson's result as being due to the fact that perihelion currently occurs in early January, close to the winter solstice (December 21), and whilst this phasal relationship has occurred it happens that the Earth's gross climate has latched onto the anomalistic rather than the tropical year as its fundamental periodicity. But the date of perihelion moves by about one day every 70 years due to precession, with the result that within a few centuries, or maybe a millennium, the dates of perihelion passage and the solstice will have separated sufficiently such that the climate cyclicity will change to the tropical year.

In the above context, one asks: what is the year length that is going to be used for this 10,000 year clock, then?

But it gets more complicated. If one looks at the official publications of the US and UK governments (per the US Naval Observatory and the Royal Greenwich Observatory: e.g., the Explanatory Supplement to the Astronomical Almanac, revised 1992) regarding timekeeping, one will find that the (mean) tropical year is incorrectly defined, and thus misleading. From the aspect of the calendar, however, the mean tropical year is irrelevant. The US and the UK use a calendar which happens to coincide with the Gregorian calendar (I would argue as to whether it is IDENTICAL with the GC because the definition, in Lord Chesterfield's Act of 1751, does not mention the GC although it defines leap years in the same way; a specific difference is that the Easter computus is not the same algorithm as that used by the Catholic Church although it leads to the same result). But the aim of the Gregorian Calendar was to keep the Vernal Equinox on about the same date, so as to regularize the Easter computus. The appropriate year length to use is therefore the time between Vernal Equinoxes and this is NOT the same as the mean tropical year, which might be thought of as being the long-term average of the four distinct years resulting from considerations of the times between vernal equinoxes, autumnal equinoxes, summer solstices, and winter solstices. These are all different, and varying due to the precession of the Earth's non-circular orbit. If you are interested in setting up a 10,000 year clock, the changes are going to be very significant indeed, and not predictable due to various things (lunar and planetary perturbations, for example).

In all of the above I have talked about year lengths in 'days'. In fact our fundamental unit of time is the second, which is now defined using atomic clocks, and referred to the day length at the start of the year 1900. Actually our days are getting longer due to tidal drag, and that is why leap seconds need to be inserted into some years (one to be inserted at the end of December 31st this year was gazetted just a couple of days ago). Over a period of centuries or millennia this slow-down of the Earth's spin is very significant: some hours over a couple of thousand years. For example, we have records of solar eclipses seen from (say) Athens or Rome in the first millennium BC which would have produced ground tracks thousands of kilometres away if the Earth had a constant spin rate. One cannot say what the change in the spin rate (and orientation) of our planet will be in the future, because there is an erratic component superimposed on the overall trend. There are seasonal changes, and others due to vagaries of the climate (which changes the angular momentum of the atmosphere). Certainly over 10,000 years one expects an accumulated spin deficit of order a day, but one cannot predict it to better than a few hours.

All of the above matters I discuss in much more detail in my forthcoming book MARKING TIME (Wiley, 1999).

I recognize that IN PRINCIPLE one could set up a self-correcting clock to accommodate corrections necessitated by the above considerations (and there are others). Stewart Brand mentioned the possibility of the clock observing the Sun every so often so as to correct itself, but it would also need to make observations of the moon and stars. Indeed our best knowledge on the variation in the rate and orientation of the terrestrial spin comes from Very-Long Baseline (radio) Interferometry using distant quasars. I would think that even Charles Babbage would have doubts as to whether one could accomplish such things with a purely mechanical system.

Duncan Steel

DUNCAN STEEL, research astronomer at the Anglo-Australian Observatory and a research fellow at the University of Adelaide, Australia, is the author of Rogue Asteroids and Doomsday Comets.

SULLOWAY CITATIONS AND NOTES
BIRTH ORDER AND THE NURTURE MISASSUMPTION: A REPLY TO JUDITH HARRISBy Frank Sulloway

LITERATURE CITED

Blanchard, Ray. Birth order and sibling sex ratio in homosexual versus heterosexual males and females. Annual Review of Sex Research, 8:27-67.

Costa, Paul T., Jr., and McCrae, Robert R. 1992. NEO PI-R Professional Manual. Odessa, FL: Psychological Assessment Resources.

Ernst, CÇcile, and Jules Angst. 1983. Birth Order: Its Influence on Personality. Berlin and New York: Springer-Verlag.

Harris, Judith Rich. 1995. Where is the child's environment? A group socialization theory of development. Psychological Review, 102:458-89.

Harris, Judith Rich. 1998. The Nurture Assumption: Why Children Turn Out the Way They Do. New York: Free Press.

Loehlin, John C. 1997. A test of J. R. Harris's theory of peer influences on personality. Journal of Personality and Social Psychology, 72:1197-1201.

Modell, John. 1996. Family niche and intellectual bent. Review of Born to Rebel, by Frank J. Sulloway. Science, 275:624.

Rosenthal, Robert. 1987. Judgment Studies: Design, Analysis, and Meta-analysis. Cambridge: Cambridge University Press.

Salmon, Catherine A. 1998. The evocative nature of kin terminology in political rhetoric. Politics and the Life Sciences, 17:51-57.

Salmon, Catherine A. In press. On the impact of sex and birth order on contact with kin. Human Nature.

Salmon, Catherine A., and Daly, Martin. 1998. Birth order and familial sentiment: Middleborns are different. Human Behavior and Evolution, 19:299-312.

Sulloway, Frank J. 1995. Birth order and evolutionary psychology: A meta-analytic overview. Psychological Inquiry, 6, 75-80.

Sulloway, Frank J. 1996. Born to Rebel: Birth Order, Family Dynamics, and Creative Lives. New York: Pantheon; Vintage, 1997.

Sulloway, Frank J. In press. Birth order, sibling competition, and human behavior. In Paul S. Davies and Harmon R. Holcomb III, eds., The Evolution of Minds: Psychological and Philosophical Perspectives. Dordrecht and Boston: Kluwer Academic Publishers.

NOTES

1. An important exception to this statement involves research on homosexuality, where birth order has been implicated in the build-up of antibodies to one of the minor histocompatibility antigens (Blanchard 1997). This apparent biological source of birth-order affects in psychosexual behavior applies only to a small portion of the population and appears to have no measurable influence on normal individuals.

2. I do not bother to address here Harris's claim that birth-order effects are less frequent in large studies because she bases this argument on data that are contaminated with errors.

3. Of course, it is inconsistent for Harris to code her results in terms of "studies" — purportedly to eliminate multiple findings that are not statistically independent--and then to fall back on the claim that these results cannot be tested statistically because they contain findings that are not statistically independent. It is also relevant to compare Harris's meta-analytic findings regarding Ernst and Angst's (1983) list of studies with her erroneous statement, in her 1995 article: "When the proper controls were used, no birth-order effects were found on personality" (p. 461). By Harris's own count, 49 significant confirming results are to be found in her own total of 179 controlled studies compiled from Ernst and Angst's tables, or more than ten times the rate of confirming results expected by chance.

4. Ways of resolving the file-drawer problem have attracted considerable discussion by statisticians, but Harris, having planted her seeds of doubt on this topic, chooses to pass over this literature. For example, Robert Rosenthal (1987) has suggested a "rough and ready guide" for determining whether a given number of significant findings in the published literature would be invalidated by unpublished null findings in file drawers. This test involves calculating the number of null findings that would have to exist in file drawers in order to cause the number of significant published findings to no longer exceed chance expectations. This number is 19S-N, where S is the number of significant findings and N is the number of nonsignificant findings. Specifically, Rosenthal's formula requires the existence of 1,244 null findings from controlled birth-order studies to invalidate the results in my own meta-analysis. Rosenthal considers a meta-analysis as passing the file-drawer test if the number of null findings needed for refutation is more than 5 times the total number of findings, plus 10 (in this case, 990 findings). In short, by Rosenthal's guide, these meta-analytic counts pass the file-drawer test. This form of the file-drawer test is considerably less powerful than one based on effect sizes. A conservative version of this alternative test involves estimating effect sizes based on p-values and setting z (the effect size for each finding), to 1.645 for all results that are significant at p<.05, and to 0 for all nonsignificant results. Based on this method, the number of null findings that are required to exist in file drawers in order to invalidate the significant meta-analytic totals in my own survey is 3,171, or 16 times the number of published findings. For Harris's totals, the required number of null findings in file drawers is 1,339, or 7.5 times the number of published findings. In actuality, the number of null findings that would be required to invalidate these results is considerably greater than either of these two conservative estimates.

5. Although self-report studies manifest more significant birth-order differences than would be expected by chance, many of these studies — even large ones — report small and nonsignificant effects. Judith Harris likes to cite Jules Angst's large birth-order study involving 7,582 college-age Swiss subjects, which found only one significant difference among the 12 scales he and his colleagues employed. These admittedly modest results are probably explained by the use of unanchored scales, the omission of the most relevant scales (for example, those related to conscientiousness), and problems with scale heterogeneity (that is, combining traits such as dominance and sociability when measuring general attributes such as extraversion--see Sulloway, in press). It is noteworthy that when these Swiss investigators sampled specific behaviors among their subjects, they obtained strikingly different results from those based on their self-report personality test. For example, laterborns were significantly more likely than firstborns to admit having experimented with drugs, including tobacco, alcohol, marijuana, tranquilizers, and hypnotics. In addition, firstborns were significantly more likely than laterborns to discuss their problems with their parents. Harris fails to cite these significant findings.

6. Firstborns and laterborns differed significantly on each of the six votes within the Convention; on the decision to sign, or not to sign, the protest petition; and on the composite scale for tough-mindedness.

7. Firstborn and laterborn scientists differed significantly on all five measures, which are similar, moreover, to measures of openness to experience employed on standard personality tests, such as the NEO PI-R (Costa and McCrae 1992).

8. These birth-order effects explain 4.2 percent of the variance in personality, after being controlled for age, sex, sibship size, and social class. This degree of influence is equivalent to a medicine that would increase one's chances of surviving a deadly disease from 40 percent to 60 percent, or a 50 percent increase over the base rate. It is worth noting that the shared family environment, which explains about 5 percent of the variance in personality, involves an even larger contribution to personality. Harris, who does not properly explain to her readers the real-world meaning of such modest "effect sizes," repeatedly describes the influence of the shared family environment as negligible, as with the following statement: "The data [from behavioral genetic studies] showed that growing up in the same home, being reared by the same parents, had little or no effect on the adult personalities of siblings. Reared-together siblings are alike in personality only to the degree that they are alike genetically" (1998:37). Added together, these two sources of environmentally explained variance (stemming from parents and siblings) total more than 9 percent, which is nearly a quarter of the entire amount of variance (40 percent) that is actually available for explanation. Based on these data alone, one could write a persuasive book about the influence of the family on personality, and these data are not even the whole story, because they do not include other within-family influences. In particular, parents have a much greater influence on the social attitudes and values of their offspring than they do on personality.

In a recent test of Harris's group socialization theory, Loehlin (1997) found that shared peer groups among late-adolescent twins explained only 2.6 percent of the variance in personality, whereas Harris's theory demands that it account for the bulk of the variance that is available for explanation (about 35 percent). Loehlin's study also demonstrated a role for parental treatment on personality, which, in his study, explained about 1 percent of the variance. Although Loehlin was not able to test for the role of shared peer groups in early and middle childhood, his findings can be extrapolated from another of his measures and are not particularly encouraging for Harris's theory. In short, peer groups seem to matter (certainly a reasonable proposition), but they do not appear to provide anything like the whole story about environmental influences, as Harris would have us believe.

9. The correlation between the two relevant sets of effects sizes (for siblings and spouses) is .73 (N=30 traits, p<.001).

10. The consistency of birth-order effects among roommates, compared with those found by direct sibling comparisons, is given by the correlation between these two sets of effect sizes--namely, .87 (N=25 traits, p<.001). With peer ratings, birth-order effects in my study are also statistically significant, although they are smaller than those effects observed among siblings, spouses, and roommates. This is to be expected because the reliability of peer ratings is substantially lower than for spouses and siblings (and presumably for roommates), thus attenuating correlations with birth order.

11. In addition to their findings about middle children, Salmon and Daly (1998) have also replicated my findings about birth order and attitudes toward radical change. They asked 100 middle-aged Canadian subjects, "Do you think that you are open to new and radical ideas (such as cold fusion)?" Of the firstborn respondents, 47 percent answered "yes" to this question, whereas 86 percent of the middle children answered in the affirmative, and 89 percent of the lastborns did so (partial r=.38, p<.001, controlled for age, sex, and sibship size).