Research on Child Development:
What We Can Learn from Medical Research
by Judith Rich Harris
(Invited talk given at a meeting of the Children's Roundtable,
Brookings Institution, Washington, DC, September 28, 2000)
Let me begin with a quote from a book on clinical epidemiology
by Alvan Feinstein:
In medical science, almost every plausible concept that has been
held throughout the centuries about the causes, mechanisms, and
treatment of diseases has been either wholly wrong or so deficient
that it was later overthrown and supplanted by other concepts.
(Feinstein, 1985, p. 409).
The erroneous beliefs were overturned only when medical
researchers finally put them to the test, by doing the right
experiments. But even when the right experiments are done, it's very
difficult to overthrow deeply entrenched beliefs. Quoting Feinstein
When the conclusion suggested by the research is compared with
the belief held by the reader or by the scientific community, all
further aspects of rational analysis may vanish. If the results
confirm what we believe, the customary human tendency is to assume
that they must be right. The research methods need not be examined
closely because there is no need to do so. Having produced the right
answer, the methods must also be correct. Conversely, if the results
are contrary to what we believe, the research methods must be wrong,
no matter how good they seem. . . . The greater or more entrenched
the paradigm that is threatened by the research, the more likely is
the reader to resist accepting the results and the more likely is
the investigator to be assailed not merely for flawed research but
also for flawed intellect or character. (Feinstein, 1985, p.
No doubt you can think of examples of this kind of resistance.
If not, you're out of luck, because that's not what I'm going to
talk about today. I want to talk about the other half of Feinstein's
statement: the fact that when data are consistent with deeply
entrenched beliefs, the research methods aren't examined closely
The deeply entrenched belief I have in mind, of course, is the
nurture assumption -- the assumption that the environment provided by
parents has important effects on how their children turn out. In my
book, and in an article scheduled to appear in the November 2000
issue of Developmental Psychology (Harris, 2000), I pointed
out some of the
obvious errors made by researchers in their eagerness to accept any
evidence that appears to support their faith in the nurture
Now I'd like to tell you about some of the less obvious errors.
My short-term goal is to convince you that research that appears to
support cherished beliefs must be examined as carefully as research
that conflicts with those beliefs. My long-term goal is to enlist
your aid in reforming the way research in developmental psychology
is funded, carried out, reported, and applied. This is not just a
scientific issue -- it's an economic issue as well. When time and money
are wasted on useless research, it means that less time and money
are available for research that might prove useful.
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:
Exhibit A: the work of Harvard's [Jerome] Kagan. He has shown
how different parenting styles can shape a timid, shy child who
perceives the world as a threat. Kagan measured babies at 4 months
and at school age. The fearful children whose parents
(over)protected them were still timid. Those whose parents pushed
them to try new things -- "get into that sandbox and play with the
other kids, dammit!" -- lost their shyness. A genetic legacy of
timidity was shaped by parental behavior, says Kagan, "and
these kids became far less fearful." (Begley, 1998, p. 56)
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
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.:
Genetically reactive young animals that are reared by calm
mothers for the first six months of their lives and then placed in
large social groups made up of peers and nonrelated older adults
develop normally and indeed rise to the top of their dominance
hierarchy. . . . By contrast, genetically reactive infants who are
reared by reactive mothers typically are socially incompetent when
placed in the larger living group at the age of six months and are
particularly vulnerable to stress. (Collins et al., 2000, p.
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
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.
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
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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