Let's look first at some of the research that has been used by developmentalists to convince journalists or other psychologists that I don't know what I'm talking about and that I have ignored studies that don't fit my thesis. Here's what Newsweek magazine labeled "Exhibit A" in its short list of studies I've supposedly ignored:

The problem is that the research described here, if it exists, has never been published. The only support I've been able to find for the statement that Newsweek attributed to Kagan is one unpublished doctoral dissertation that followed 24 babies to the age of 21 months, plus one other study that followed children to the age of 3. Nothing that followed children to school age, as Newsweek claimed, or even to sandbox age.

The doctoral dissertation is by Doreen Arcus, one of Kagan's students. It's still unpublished, nearly ten years after it was handed in, but it's often cited (as Arcus, 1991, or as Arcus, Gardner, & Anderson, 1992). As far as I've been able to determine, it's the only evidence Kagan and his students have managed to produce, in more than 20 years of studying fearful children, to support their belief in parental influences on fearfulness. Arcus found a positive correlation between overprotective parenting in infancy and fearfulness at age 21 months. The correlation at age 3 was found, for boys only, by another group of researchers, Park, Belsky, Putnam, and Crnic (1997).

Assuming that this finding can be extended to older children of both sexes, what would it prove? Only that anxious, fearful parents tend to produce anxious, fearful offspring. Such traits are heritable -- Kagan himself (1994, p. 168) reported estimates of .50 to .70 for the heritability of fearfulness -- and therefore children born with a predisposition to be anxious or fearful are more likely to be reared by anxious, fearful parents (and vice versa). We can get a more accurate estimate of environmental influences on this personality trait by looking at adopted children. Adoption studies provide no support for the belief that the parents' child-rearing style has an influence on the adoptee's adult personality (Plomin, DeFries, McClearn, & Rutter, 1997).

The problem with adoption studies, though, is that they give you only the bottom line: the net result of all the environmental influences shared by children reared in the same home. In other words, main effects. Main effects attributed to parenting go up in smoke if the method provides an adequate control for genetic influences, and that's why many cutting-edge developmentalists (e.g., Collins, Maccoby, Steinberg, Hetherington, & Bornstein, 2000; Vandell, 2000) have given up looking for main effects and are instead talking about interactions.

Medical researchers sometimes do the same thing, when results turn up that are not to their liking. In April of this year, the New England Journal of Medicine reported the results of a randomized, controlled test of bone marrow transplants for patients with advanced breast cancer (Stadtmauer, 2000). The results were disappointing: the patients who received a bone marrow transplant plus chemotherapy did not live any longer than those who received chemotherapy alone. But physicians who had been using bone marrow transplants found it difficult to give up their faith in them. One of the co-authors of the study was quoted as follows, in a news story: "Erban said it is possible that a small set of patients might still be found who do better with the transplants" (Associated Press, 2000). In other words, even though there was no main effect -- averaged across patients, the effect on survival was zero -- perhaps there's an interaction.

For fearfulness in children, the hypothesized interaction is between the parents' child-rearing style and the child's temperament. The claim is not that parental overprotectiveness makes all children fearful -- only those born with what Kagan (1994) calls a "high-reactive" temperament.

To test this hypothesis in a systematic way, what we need is a better kind of adoption study -- not one in which high-reactive babies are handed out at random, but one in which they're distributed systematically, half to nervous parents, half to calm ones. Of course, we can't do a study of this sort with human babies, but it can be done with rhesus monkeys. In fact, it has been done, according to an article in the February (2000) issue of American Psychologist: "Contemporary Research on Parenting: The Case for Nature and  Nurture," by Collins, Maccoby, Steinberg, Hetherington, and Bornstein. According to this article, primatologist Stephen Suomi did a "cross-fostering experiment" in which high-reactive baby monkeys were reared either by nervous or calm mothers. Here are the results, as reported by Collins et al.:

That sounds impressive: young monkeys showing the effects of maternal rearing style long after they had been separated from the mothers who reared them -- a clear contradiction of my theory. But Suomi's study of cross-fostered baby monkeys is an excellent example of research that hasn't been examined closely enough because it fits so well with entrenched beliefs.

The reference cited by Collins et al. for the cross-fostered monkeys was Suomi, 1997 -- a chapter in an edited book. But that chapter contains no mention of the cross-fostering experiment. Eventually I traced the story of the cross-fostered monkeys back to a 1987 paper by Suomi -- another chapter in an edited book. In it, Suomi described a study -- more precisely, the beginnings of a study -- in which high-reactive and low-reactive infant monkeys were systematically cross-fostered to mothers who varied along two dimensions: calm vs. nervous and nurturant vs. punitive. "Unfortunately," Suomi reported, in that first sample "there were not enough infants and foster mothers to fill all cells of the 2 x 2 x 2 . . . design matrix" (1987, p. 406). He never gave the N, but evidence in that chapter (1987, pp. 405-414) and in a later article (Champoux, Boyce, & Suomi, 1995) led me to conclude that the number of cross-fostered monkeys in that sample was probably seven. If I am correct in this conclusion, it would mean that there probably were no more than four high-reactive baby monkeys, of which two may have been reared by calm foster mothers.

Dr. Suomi has told me (personal communication, March 1, 2000) that he has collected data from a considerably larger sample of cross-fostered baby monkeys, over a four-year period (which began before 1987 and which therefore must have ended before 1991). But the relevant data from the larger sample have never been published anywhere, and the data from the original sample have never been published in a peer-reviewed journal. Suomi has referred to the cross-fostered baby monkeys many times in his later talks and writings, but he cites either his 1987 chapter or a 1991 chapter that contains no new data on cross-fostered monkeys but instead refers back to the 1987 chapter; in fact, the graphs from the 1987 chapter are reproduced unchanged. What does it imply, when early results are published informally and imprecisely, and later results from a larger sample aren't published at all?

[Author's note added in August, 2002. Suomi described his cross-fostered monkeys -- the ones who turned out well because they were reared by the right kind of foster mothers -- in the talk he gave at a conference sponsored by the National Institute of Child Health and Human Development, in August 1999. However, those cross-fostered monkeys are conspicuously absent from Suomi's (2002) chapter in the book based on the conference, submitted after I began to raise questions about his data.]

In their paper in American Psychologist, Collins, Maccoby, Steinberg, Hetherington, and Bornstein (2000) gave the impression that the cross-fostering experiment was a well-established, published finding -- not a pilot study involving a very small number of high-reactive baby monkeys. They made other errors as well. For example, they said that Suomi found that the effects of early rearing experience were "especially perceptible" under stressful conditions (Collins et al., p. 224). But Suomi actually reported that genetic differences among the cross-fostered monkeys were especially perceptible under stressful conditions -- the temperament of their foster mothers was "essentially irrelevant" for predicting how they would react under the stress of temporary separations (Suomi, 1991, p. 53). Furthermore, Collins et al. reported that high-reactive baby monkeys reared by calm foster mothers had done well in their later lives, but what Suomi actually said was that high-reactive monkeys reared by nurturant mothers had done well (1991, pp. 53-54).

Nurturant, not calm. Does that sound like a quibble? Well, it turns out that Suomi's "nurturant" foster mothers are the precise simian equivalents of Kagan's "overprotective" human mothers. But the high-reactive baby monkeys reared by nurturant mothers did very well, whereas the high-reactive baby humans reared by nurturant mothers did poorly.   In other words, these two studies -- Suomi's (1987, 1991) and Kagan's (1994, based on Arcus, 1991) -- both involve interactions between the infant's temperament and the mother's protectiveness and thus appear to support each other, but in fact they conflict with each other. The conflict wasn't apparent because Collins et al. (2000, p. 224) said "calm mothers" instead of "nurturant mothers." (Coincidentally, the action editor for the article by Collins et al. was Jerome Kagan.)

I turn now to the kind of study that has made medical research so successful: the experimental study with a randomized control group. Over the years, medical researchers have learned the hard way that researcher biases can influence results, and they've developed elaborate procedures for guarding against them -- blinded collection and analysis of data, ways of making sure that the assignment of participants to experimental and control groups is truly random, and so on. Such precautions should be used in psychology too, but they generally aren't.

In developmental psychology, experiments usually take the form of interventions. The researchers, and the granting agencies that finance the research, are united in the hope that the intervention will prove to be beneficial. In fact, researchers whose interventions fail to produce beneficial effects might have trouble getting their grants renewed. Medical researchers are expected to disclose any financial ties they have to the manufacturer of a drug they are testing, but similar conflicts of interest occur all the time in psychology, and nobody raises an eyebrow.

Conflicts of interest often lead to publication bias, the tendency for significant or favorable results to be published and non-significant or unfavorable results not to be published. Medical researchers use something called a funnel plot (e.g., McAlindon, LaValley, Gulin, & Felson, 2000) to test for publication bias in a meta-analysis. The number of participants in each study is plotted against effect size. If effect sizes tend to be larger for studies with small samples, it's an indication of a publication bias. The reasoning is that a big study is likely to be published regardless of its outcome, whereas if a small study doesn't produce the desired effect, the researchers simply shrug and toss it out. Though I didn't realize it at the time, I demonstrated a publication bias for birth order studies in Appendix 1 of my book (Harris, 1998), when I showed that large studies were less likely than small ones to report significant birth order effects.

But even a large sample size is no guarantee that a study will be published, if it fails to produce the expected results. A developmentalist once told me in e-mail that, some years back, she and a well-known colleague had done a "very elaborate and expensive" parent-training intervention that had yielded "NO effects." The study was never published and I doubt it ever will be, because her colleague has since died.

Now we come to more subtle sources of bias. In my forthcoming paper in Developmental Psychology (Harris, 2000), I mentioned an intervention study by Forgatch and DeGarmo (1999). The intervention was designed to improve the mothers' child-rearing methods and it succeeded in doing so -- on average, the mothers in the intervention group used less "coercive parenting" and showed more "positive involvement" than those in the control group. The question is, did this favorable change in the atmosphere of the home produce an improvement in the child's behavior in school? My theory predicts that a home-based intervention of this kind will have no effects on the child's behavior in school, and Forgatch and DeGarmo's results were consistent with my prediction: they found no significant differences in school behavior between the control group and the intervention group.

Unwilling to take no for an answer, Forgatch and DeGarmo (1999) did a post-hoc data analysis -- a path analysis. The path analysis gave them the results they were looking for: it showed that those mothers who improved in their child-rearing methods were more likely to have children who behaved well in school.

It's easy to see why this kind of analysis would make sense to a developmentalist. The author of another intervention study patiently explained it to me in e-mail, in capital letters:

The problem is that the path analysis introduces a bias that Feinstein (1985), the epidemiologist, calls "a compliance-determined susceptibility bias." "A particularly tricky problem occurs," Feinstein says, "if compliance depends on certain personality traits that may also be associated with the outcome event" (p. 303). He gives a true example: a randomized trial of a drug designed to reduce blood lipids. The trial showed that the patients who complied well with the drug regimen had significantly lower fatality rates than patients who complied poorly. The catch was that the patients who received only a placebo but who complied well with the regimen also had significantly lower fatality rates!

People who comply with interventions are likely to differ in personality and intelligence from those who do not comply. Because these characteristics are heritable, parents who respond well to the demands of an intervention are more likely to have children who respond well to the demands of school. Assignment to the intervention or control group is supposed to be random. The path analyses used by Forgatch and DeGarmo (1999), and by Cowan and Cowan in a new intervention study that will be published in 2002, are equivalent to letting the participants decide for themselves which group they will be in.

Cowan and Cowan presented their results at a 1999 conference called "Parenting and the Child's World: Multiple Influences on Intellectual and Socio-Emotional Development," sponsored by the National Institute of Child Health and Human Development. Now NICHD is planning to follow up the conference by putting out a pamphlet of child-rearing recommendations to parents; the participants in the conference have been invited to contribute their advice (Azar, 2000).

I find the production of this pamphlet troubling. At the conference (which I attended), most of the participants spoke enthusiastically about looking for interactions between parenting style and the child's temperament; they no longer seemed certain that parenting has any main effects. The new motto is: different children react differently to a given style of parenting. Yes, I'm sure they do, and it may also be the case that different breast cancer patients react differently to bone marrow transplants. But the physician who said that bone marrow transplants might have a beneficial effect on some subset of patients would be acting irresponsibly if he recommended that treatment to all his patients. He'd have to know which subset might be benefitted and which might be harmed. Do the developmentalists have the knowledge to say which subset of children might be benefitted, and which might be harmed, by a given style of child-rearing? If not, how can they make recommendations to parents?

But I don't want to leave you with the impression that I think interventions are a waste of time and that parents are powerless. Interventions aimed at children can work, if they're well designed. Parents can have a lot of power under some conditions. In the time that remains, I'd like to sketch out some issues I think are important in designing interventions and in giving parents more power.

If an intervention improves the parent-child relationship and makes life at home pleasanter for the parent and the child, then it has accomplished something worthwhile. But it's unrealistic to expect a home-based intervention to improve the child's behavior at school. To improve the child's behavior at school, we need school-based interventions. My theory predicts that such interventions are more likely to have lasting effects if they're aimed at a group of children -- children who see each other day in and day out, not just during the intervention -- and if the children remain in contact with each other after the intervention ends. Another prediction -- this one has recently been confirmed by Dishion, McCord, and Poulin (1999) -- is that it is dangerous to put together antisocial or aggressive kids for a group intervention. Such kids have to be discouraged from forming their own groups.

I said that parents can have a lot of power under some conditions. The reason they have power is that children learn things from their parents! Moreover, children retain much of this learning, even when they go outside the home. They retain it because they find it useful -- it agrees with what they find out there. For example, most children in the United States learn their first language at home -- they learn it from their parents. If that language happens to be English, they will continue to use it.

Parents who speak a language other than English, or who belong to a culture other than the majority culture, are aware that their children are likely to abandon that language and culture if they're reared in the United States. But some parents have found ways of keeping their language and culture alive in their children. One way they can do it is by settling in a neighborhood where there are many immigrants who share their native language and culture. Another way is to make sure that their child's schoolmates are being reared by parents who have the same goals that they do. This is the method used by groups such as the Hutterites and the Hasidic Jews (see Harris, 1998). By maintaining their own schools, they determine who their children's schoolmates will be. Parents do the same thing when they choose among child-care options for their preschoolers. They want their children's playmates to come from families with the same attitudes and customs as their own.

Parents who want to preserve their language and culture have a third alternative -- a part-time method. Many Chinese families send their children to weekly classes where they learn about the Chinese language and culture in the company of other Chinese-American children. There are summer camps for the children of Muslim, Hindu, and Sikh parents who want to preserve their culture and religion (Goodstein, 1998). There's even a summer camp for children whose parents want them to learn Yiddish (Matchan, 1999). These parents had discovered that it was a losing battle to try to teach their kids Yiddish by speaking it to them at home, but the kids picked it up quickly when they were able to use it with other kids whose parents also wanted them to learn Yiddish.

In psychology, interventions usually have the goal of changing the social behavior of the participants. Because language is a social behavior, it is informative to look at two interventions that had the ambitious goal of bringing about a change in language -- in one case, by creating a new language (Esperanto) and persuading people to use it; in the other, by reviving a language (Hebrew) that had been used only for liturgical purposes for two millennia.

There are hundreds of thousands of Esperanto users in the world. There are Esperanto clubs and Esperanto magazines; some users even teach the language to their children (Janton, 1993). And yet, as an intervention, the Esperanto movement failed. There are few, if any, native speakers of Esperanto; it remains a second (or third or fourth) language for the highly motivated adults who speak or write it.

On the other hand, the attempt to revive Hebrew succeeded, even though modern Hebrew -- the product of many arbitrary decisions regarding pronunciation, vocabulary, and so on -- is in some ways as artificial a language as Esperanto. The revival of Hebrew is traditionally credited to Eliezer Ben-Yehuda (1858-1922), who demonstrated the viability of the language by producing the first "native" Hebrew speaker in two thousand years: his son. Ben-Yehuda and his wife spoke nothing but Hebrew to the child, so of course the child learned Hebrew. But as an interventionist, Ben-Yehuda was no more successful than the people who taught Esperanto to their children. According to Harshav (1993), "Ben-Yehuda had no real influence on the revival itself" (p. 84). Hebrew didn't make much headway until twenty-five years later, when a wave of idealistic new immigrants arrived in Palestine and formed little communities. The communities created schools, and the children who went to these schools were taught Hebrew. Hebrew became their "native language," though it wasn't the native language of their parents, because it was the language they used with each other (see Bickerton, 1983). The successful interventionists were the parents who created these schools and the teachers who taught in them.

Parents have a great deal of power when they get together with the parents of their children's peers. Studying how and when they exert this power can help us to design effective interventions. Even home-based interventions might work, if they reached the majority of parents of a given group of children.

To find out how the environment affects the child, we need research methods capable of providing unambiguous answers to our questions, because ambiguous answers tend to be seen as confirmation of entrenched beliefs. I'm sure the members of the Roundtable are well aware of the need to distinguish between the effects of the parents' genes and the effects of the environment provided by the parents -- effects that are often confounded because they're correlated with each other. What you might not be aware of is the need to distinguish between the effects of the home and the effects of the school or the community. These effects, too, are often confounded because they're correlated with each other.

In the long run, I believe that the school and the community are going to have a greater impact on children's lives than what happens to them at home. If we want to improve the outlook for children, we are going to have to improve the schools and the communities in which they grow up.

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