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Content uploaded by Lynn Waterhouse
Author content
All content in this area was uploaded by Lynn Waterhouse on Feb 09, 2014
Content may be subject to copyright.
WATERHOUSEINADEQUATE EVIDENCE
Inadequate Evidence for Multiple Intelligences,
Mozart Effect, and Emotional Intelligence Theories
Lynn Waterhouse
Child Behavior Research
The College of New Jersey, Ewing
I (Waterhouse, 2006) argued that, because multiple intelligences, the Mozart effect, and emo
-
tional intelligence theories have inadequate empirical support and are not consistent with cog
-
nitive neuroscience findings, these theories should not be applied in education. Proponents
countered that their theories had sufficient empirical support, were consistent with cognitive
neuroscience findings, and should be applied in education (Cherniss, Extein, Goleman, &
Weissberg, 2006; Gardner & Moran, 2006; Rauscher & Hinton, 2006). However, Gardner and
Moran offered no validating evidence for multiple intelligences, Rauscher and Hinton con
-
cluded that “listening-to-Mozart” studies should be disregarded, and Cherniss, Extein,
Goleman, and Weissberg agreed that emotional intelligence lacked a unitary empirically sup-
ported construct. My reply addresses theory proponents’ specific criticisms of my review and
reasserts my original claims.
In “Multiple Intelligences, the Mozart Effect, and Emotional
Intelligence: A Critical Review” (Waterhouse, 2006), I ar-
gued that “MI theory has no validating data … the Mozart ef-
fect theory has more negative than positive findings, and EI
theory lacks a unitary empirically supported construct.” I
also argued that these theories’ brain system claims were not
consistent with relevant cognitive neuroscience findings and
concluded that until these theories have garnered reasonable
evidentiary support they should not be applied in education.
Theory proponents counterargued that their theories were
well supported by both behavioral research and cognitive
neuroscience findings and should continue to be applied in
education (Cherniss, Extein, Goleman, & Weissberg, 2006;
Gardner & Moran, 2006; Rauscher & Hinton, 2006).
Gardner and Moran (2006) affirmed the importance of
empirical evidence for multiple intelligences (MI) theory,
stating that “Theories such as evolution or plate tectonics or
MI develop through the continuing accumulation of evi
-
dence.” They claimed that abundant empirical evidence for
MI theory existed in the studies Gardner relied on to develop
his theory, but this claim conflates theory generation and the
-
ory validation. They also claimed that evidence for cognitive
systems such as reasoning and natural kind categorization of
-
fered support for MI theory, but they provided no proof for
this assertion.
Rauscher and Hinton (2006) conceded that “listen-
ing-to-Mozart” studies do have too many negative findings to
warrant being applied to the classroom. They argued instead
that skills developed in playing a music instrument transfer to
spatial skills, and thus music instruction studies have find
-
ings that are important for education. However, the concept
of transfer lacks adequate empirical support (Barnett & Ceci,
2002; Mayer, 2004; Perruchet & Vinter, 2002).
Cherniss et al. (2006) agreed that “conflicting constructs
continue to characterize EI theory,” but they viewed these
conflicts as a sign of vitality. Cherniss et al. also argued that
EI had significant predictive validity but they provided lim
-
ited evidence to support this claim.
In the discussions that follow I address theory proponents’
criticisms of my review and offer arguments to explain prob
-
lems I found in their criticisms.
MI THEORY LACKS VALIDATING
EMPIRICAL EVIDENCE
Gardner and Moran (2006) asserted that I erred in claiming
that MI theory lacked empirical support, that I misconstrued
the conceptual basis of MI, that I misunderstood the defini
-
tions of several intelligences, and that I had a naïve view of
science that limited my ability to value Gardner’s MI theory.
EDUCATIONAL PSYCHOLOGIST, 41(4), 247–255
Copyright © 2006, Lawrence Erlbaum Associates, Inc.
Correspondence should be addressed to Lynn Waterhouse, Child Behav
-
ior Research, The College of New Jersey, 234 Bliss Hall, Ewing, NJ 08628.
E-mail: lynwater@tcnj.edu
The following discussions respond to these criticisms and
outline two important evidence problems that Gardner and
Moran failed to address.
Gardner and Moran’s Proposed Evidence Does
Not Validate MI Theory
Gardner and Moran (2006) offered four evidentiary claims
for MI theory. First, they claimed that MI theory was empiri
-
cally validated by the fact that “Gardner combined the empir
-
ical findings of hundreds of studies from a variety of disci
-
plines” to develop MI theory. However, theory validation is a
process distinct from theory generation. The studies Gardner
read that led him to hypothesize that there might be MI may
serve to warrant the reasonableness of his hypothesis, but the
studies he read cannot validate the existence of MI.
Second, Gardner and Moran (2006) argued that MI
subcomponents were supported by empirical evidence for
“manyspecificneuralsystems …liketheoryofmind,recogni
-
tion of natural kinds, understanding of self, understanding of
others,” andbyevidencefor “systems of numerical, linguistic,
and causal reasoning.” Gardner and Moran further argued that
“modules identified by evolutionary psychologists, contrary
to Waterhouse’s argument that they refute MI theory, actually
align very well with Gardner’s intelligences and their
subcomponents.” However, Gardner and Moran did not sup-
plya crucialspecification:Whichmultiple intelligence is sup-
ported by what evidence for which neural system or adapted
cognition module? For example, Astuti, Solomon, and Carey
(2004) reported findings for studies of natural kind conceptu-
alization in Madagascar. Natural kind conceptualization in-
cludes, among other things, seeing objects, animals, and other
humans; labeling objects and individuals; grouping objects
and individuals;and conceptualizing categories of groupings.
Consequently, Astuti et al.’s evidence for natural kind catego
-
rization“alignswith”atleast fourintelligences: thevisualspa
-
tial intelligence, the naturalistic intelligence, the linguistic in
-
telligence, and the interpersonal intelligence.
Examination of individual adapted cognition modules and
cognitive systems revealed that their specific behavioral
components aligned with more than one multiple intelli
-
gence (Waterhouse, 2006), thus cutting across the boundaries
of Gardner’s intelligences. Consequently this evidence does
not provide empirical support for the intelligences but, con
-
versely, argues against the framework of MI.
A related problem is that neither Gardner nor any of his
adherents has defined a set of testable psychological
subcomponents for each of the intelligences (Allix, 2000).
Gardner (2004) asserted that because his “basic paradigm
clashes with that of psychometrics” (p. 214), and because
testing “results may well be misused,” he will not define
testable subcomponents for the intelligences. Without such
subcomponents, the intelligences are defined only by gen
-
eral descriptions (Gardner, 1983, 1999, 2004), and the gen
-
erality of these descriptions has prevented researchers from
conducting studies to explore the validity of the
intelligences (Allix, 2000).
Gardner and Moran’s (2006) third evidentiary claim was
that Gardner, Feldman, and Krechevsky (1998) reported em
-
pirical evidence for multiple intelligence profiles in pre
-
school children. However, this 1998 report is inadequate as
support for MI theory. No formal data analysis was pre
-
sented, and the half-page discussion of findings is too brief
and too vague to be used by other researchers:
Assessments did identify distinctive profiles for a majority of
children … every child exhibited at least one strength …
there was little correlation between the children’s perfor
-
mances on the different activities … because of the small
sample size (39 subjects), our results must be regarded as ten
-
tative. (Gardner et al., 1998, p. 27)
Fourth, Gardner and Moran (2006) claimed that MI theory
will ultimately accrue evidence comparable to that for evolu
-
tionary theory and plate tectonics theory. Even though only
23 years have elapsed since Gardner first proposed MI
(1983), Gardner and Moran’s claim can already be seen to be
mistaken. Unlike MI theory, evolutionary theory and plate
tectonics theory accrued important validating empirical find-
ings quite soon after they were proposed. In the 23 years fol-
lowing Darwin’s publication of Origin of Species in 1859
(Appleman, 2000), other scientists presented an array of fos-
sil and faunal evidence in support of Darwin’s theory
(Bowler, 1986). In the 23 years following the emergence of
plate tectonics theory in the 1960s, data collected from ocean
floor mapping, magnetic rock record measurement, radio-
metric dating of the Earth’s magnetic pole reversal history,
and precise location of earthquake sites provided strong vali
-
dating empirical evidence for plate tectonics theory
(Oreskes, 2003). MI theory has accrued no such validating
empirical evidence in the 23 years since it was proposed.
The Multiple Levels of MI
Gardner and Moran (2006) argued that I misconstrued the
intelligences as skills because I failed to “encompass the
several levels on which MI theory examines intelligences.”
Gardner and Moran proposed (a) the finer level of neuro
-
logical subcomponents of each intelligence, (b) the middle
road level of the intelligences, and (c) the broader level of
skills that use the intelligences “to produce proficient
and/or expert behavior.”
Contrary to Gardner and Moran’s (2006) claim, I did un
-
derstand these levels. My review outlined cognitive systems
of the same explanatory scope (middle road level) as MI
whose findings countered the nature and boundaries of MI
(Waterhouse, 2006). In their response Gardner and Moran re
-
defined the “What is it?” and “Where is it?” cognitive sys
-
tems down from middle road level to finer level neurological
subcomponents of the intelligences. They also redefined
248
WATERHOUSE
Kahneman’s decision-making processes up from middle
road level to broader level skills that would deploy Gardner’s
intelligences. These down-a-level and up-a-level
redefinitions had the effect of side-stepping the evidence
against MI theory that these systems provide. Moreover,
Gardner and Moran’s redefinitions were inaccurate.
What is it and where is it processing streams could
not be MI subcomponents.
The brain’s primary visual
cortex sends visual information along both the ventral (what
is it) and dorsal (where is it) processing streams, wherein
neurons further downstream to learn to respond to increas
-
ingly organized sets of features (Deco & Rolls, 2005). These
two streams begin with shared visual information, but the
dorsal stream moves to incorporate body-in-space process
-
ing, and the ventral stream moves to incorporate auditory
processing. Thus, each stream’s mixed content processing
precludes it from being construed as a subcomponent of any
individual multiple intelligence.
Kahneman’s systems could not be domain skills
deploying the intelligences.
Briefly, in Kahneman’s
(2003) prospect theory, Systems I and II governdecision mak-
ing by predicting utility value (Will this decision be good or
bad?). System I is spontaneous but rigid and is probably based
in limbic and basal ganglia neural circuits, whereas System II
is effortful but flexible and is probably based in frontal lobe
functions (Trepel,Fox,& Poldrack, 2005). System II operates
at the concept level, and System I operates both at the percept
and concept level (Kahneman, 2003). Because the percept
level is the same as Gardner and Moran’s finer level, and the
conceptlevelisthesameasGardner andMoran’smiddlelevel,
therefore neither System I nor System II could be interpreted
as broader level skills deploying the intelligences.
Understanding Definitions of
Specific Intelligences
Gardner and Moran (2006) were correct in stating that I be
-
lieved Gardner (2004) had proposed two additional types of
intelligence. Although Gardner may have intended some
-
thing different, nonetheless both the content and parallel
structure of his published text argue that there are two MI
profiles, each yielding a separate form of intelligence. The
text posits that individuals with high IQs have “a mental
searchlight” (intelligence), whereas individuals with jagged
MI profiles have “a laser-form of intelligence” (Gardner,
2004, p. 217).
Gardner and Moran (2006) argued that I was wrong to
state that intrapersonal and interpersonal intelligences were
combined into a personal intelligence. However, Gardner
(1983, 1999) did treat these two intelligences as part of a
larger whole of “personal intelligence” (1983, chapter 10;
1999, p. 43). For example, Gardner (1983) stated that “it is
important not to gloss over differences between the personal
and other forms of intelligence” (p. 240).
Gardner and Moran (2006) further argued that I was
wrong to include empathy for natural things as part of the
naturalist intelligence. However, Gardner (1999) proposed
that the naturalist intelligence involved biophilia, wherein
the naturalist “may well possess the talent of caring for, tam
-
ing, or interacting subtly with various living creatures” (p.
49). The word empathy does not seem to me to be wide of the
mark as a summary incorporating “biophilia” and “caring
for” and “interacting subtly.”
My View of Science is Based on the
Practice of Science
Gardner and Moran (2006) argued that I had a “ naïve view of
science” that prevented me from being able to “acknowledge
or understand the enterprise in which Gardner has been en
-
gaged.” My view of science is exemplified in my practice of
science. For example, our research group synthesized neuro
-
science and behavioral findings on attachment to theorize
that abnormalities in the neurohormone oxytocin might con
-
tribute to attachment impairments found in autism (Modahl,
Fein, Waterhouse, & Newton, 1992; Waterhouse, Fein, &
Modahl, 1996). Our group then conducted empirical studies
of this hypothesis in which we did find evidence for abnor-
malities in oxytocin in autistic individuals (Green et al.,
2001; Modahl et al., 1998). Since that time other researchers
have conducted a wide range of related research, and genetic
evidence has linked an oxytocin receptor gene with autism
(Wu et al., 2005).
In fact, Gardner and Moran (2006) argued that my view of
science is naïve because I do not view Gardner’s synthesis of
research findings as validating evidence for MI theory. Syn
-
theses are important because they can summarize the current
state of research, can identify studies that should be con
-
ducted, and can yield new theories. However, if a new theory,
such as MI theory, is generated by the synthesis of existing
findings, then that new theory requires empirical validation.
MI Theory Problems That
Gardner and Moran Failed to Address
Gardner and Moran’s (2006) response failed to address two
problems for MI theory outlined in my review. Gardner
claimed that the successful application of MI theory in edu
-
cation provided empirical support for MI theory (Gardner,
2004, p. 214; Gardner & Connell, 2000, p. 292). However,
applying MI cannot provide evidence to validate the
intelligences because the act of applying MI theory assumes
the validity of the intelligences. Gardner and Moran offered
no response to this problem.
Second, Gardner (1999) asserted that MI theory depends
on each intelligence having its own neural processing circuit,
arguing that if “musical and spatial processing were identi
-
INADEQUATE EVIDENCE 249
cally represented” in neural circuits “that fact would suggest
the presence of one intelligence, and not two separate
intelligences” (p. 99). My review outlined evidence for
shared neural circuits for the processing of many different
types of content (Waterhouse, 2006). Gardner and Moran
(2006) offered no response to this evidence.
In summary, Gardner and Moran (2006) provided no vali
-
dating research evidence for MI theory, and they sidestepped
the problem that neuroscience findings for other cognitive
systems cut across MI boundaries. They were mistaken in
their claim that a theory based on a synthesis of research re
-
quires no empirical validation, and they did not address the
problem that application research cannot validate MI theory.
Finally, although Gardner (1999) claimed that MI theory
would be nullified if the neural processing circuits for differ
-
ent contents were found to be shared (p. 99), Gardner and
Moran offered no response to evidence that neural process
-
ing circuits for different contents are shared.
THE MOZART EFFECT AND
MUSIC LESSON TRANSFER
Rauscher and Hinton (2006) argued that I misconstrued the
concept of transfer and misrepresented the contents of a re-
view article by Schellenberg (2003). Their major criticism,
however, was that I was wrong to lump listening-to-Mozart
studies together with music instruction studies because “in-
struction studies, unlike the listening studies, have profound
implications for educational practice. The following sections
address these criticisms.
Transfer From Instrument Practice to
Spatial Skills is “For Free” Learning
I argued that Rauscher’s (2002) claim that music will lead to
improvement in spatial cognition (p. 276) meant that spatial
skill improvement occurred for free. Rauscher and Hinton
countered that because I lumped listening and lesson studies
together I failed to understand that improved spatial cogni
-
tion transferred via music lessons was not for free but was,
instead, effortful, because children expended effort in prac
-
ticing their instruments. Contrary to Rauscher and Hinton’s
claim, however, transfer is not effortful, it is for free learning.
For example, if a student practiced the violin daily, and with
-
out any practice in origami paper folding, showed enhanced
origami folding skills, then no matter how effortful the violin
practice was, the paper folding skill improvement is for free
because no effort was expended in practicing origami.
More important, Barnett and Ceci (2002) reviewed re
-
search on transfer and concluded that, despite 100 years of
research, no clear evidence has emerged, and many re
-
searchers believe there is no experimental design that can
determine whether or not transfer exists (p. 634). Mayer
(2004) also reviewed transfer research and concluded that
there was no evidence for general learning transfer, and no
evidence for specific skill transfer, but there was some evi
-
dence for specific transfer of general knowledge (pp.
217–218). Perruchet and Vinter (2002) reported that “to
-
tally negative results are certainly the most frequent out
-
come” in transfer research (p. 319).
Schellenberg’s (2003) Claims Concerning Music
Lesson Effects
Rauscher and Hinton (2006) argued that I misrepresented
Schellenberg (2003) by citing his article as support for the
claim that transfer from music to spatial skill had not been
demonstrated. Rauscher and Hinton argued that
Schellenberg’s (2003) statement that “positive transfer ef
-
fects to nonmusical domains, such as language, mathematics,
or spatial reasoning could be similarly unique for individuals
who take music lessons” (p. 444) meant that transfer from
music to spatial skills had been demonstrated. However,
Schellenberg’s statement (2003, p. 444) was hypothetical, as
framed by this preceding statement: “If we suspend our dis
-
belief, however, and assume that music education affects
abilities … how could we account for this influence?” (p.
443). In fact, Schellenberg (2003) proposed that “music les-
sons … may confer benefits by providing close and extended
contact with an adult other than a parent or teacher” and that
“similar effects should be evident with … chess and draw-
ing” lessons (p. 444).
Music Instruction Studies Do Not Have
“Profound Implications” for Education
Rauscher and Hinton (2006) are to be commended as scien
-
tists for their forthright review of the evidence for their own
and others listening-to-Mozart studies. They concluded that
“Given the contradictory findings of the studies on children,
we agree with Waterhouse that educational practice should
not be influenced by this area of research.”
Rauscher and Hinton (2006) argued that music instruction
studies, by contrast, have clearly demonstrated that skills de
-
veloped in playing a musical instrument do enhance spatial
skills. They cited two published studies (Rauscher et al.,
1997; Rauscher & Zupan, 2000) and a review (Hetland,
2000). Rauscher et al. (1997) reported that, unlike the control
group, 34 young children given piano keyboard lessons
showed spatial reasoning improvement that lasted for 1 day,
and Rauscher and Zupan (2000) reported that 34 young chil
-
dren given 8 months of keyboard lessons did significantly
better in creating an object from pieces than did controls.
Hetland (2000) reviewed 15 studies of music instruction’s as
-
sociation with improved spatial skills. However, only 6 of the
15 studies were published, and 2 of these 6 were the
Rauscher studies discussed previously (Rauscher et al.,
1997; Rauscher & Zupan, 2000). Moreover, 1 of the remain
-
ing 4 published studies was not directly relevant because it
250
WATERHOUSE
used music and spatial training to enhance math skills
(Graziano, Peterson, & Shaw, 1999). Of the 3 remaining pub
-
lished studies Hetland reviewed, only 1 reported an effect
with a p value of .05 or below (Costa-Giomi, 1999).
Thus, Rauscher and Hinton (2006) claimed “profound im
-
plications for educational practice” based on three published
studies that linked music instruction to spatial skill enhance
-
ment—two of which are from Rauscher’s own group. These
studies are promising, but insufficient at present to hold “pro
-
found implications” for education.
All Forms of Music’s Effect on
Spatial Skills Should Be Considered Together
Rauscher and Hinton (2006) stated that “Waterhouse’s con
-
flating listening studies with the music instruction studies
will lead to greater misinterpretation of the research by edu
-
cators, politicians, and laypeople.” I have no wish to add to
misinterpretation of current findings, but I believe it is of
value to try to establish a comprehensive understanding of all
reported music effects on spatial cognition.
Rauscher and Hinton (2006) proposed three brain mecha
-
nisms for music’s ability to cause improved spatial cognition:
transfer, cortical arousal, and synaptic plasticity. Rauscher
and Hinton argued that music lessons provided spatial skill
transfer and cortical arousal, each of which separately con-
tributed to spatial skill improvement. They also proposed that
because rats exposed to a Mozart sonata demonstrated im-
proved maze learning and exhibited changes in brain synap-
ses (Chikahisa et al., 2006), therefore, synaptic changes
could be the cause of skill transfer.
Although current research findings do not support the no-
tion of transfer, neuroscience findings do suggest functional
connections among synaptic change, cortical arousal, repeti
-
tion, and overlapping neural circuits for different forms of
content. Brief repetition and cortical arousal confer
short-term enhancement of neural circuit activity, but
long-term motor skills, perceptual skills, and content memo
-
ries depend on synaptic and other neural changes that occur
when there has been extended repetition of in the circuitry
underwriting those skills and memories and when there has
been associated cortical arousal (Phelps, 2006; Squire &
Kandel, 2000). If there are general cross-content processing
neural circuits, formed by generalist genes (Kovas & Plomin,
2006), there may be cross-content enhancement of memory.
Consequently, from what is known, the following specu
-
lative model could be proposed. Short-term exposure to mu
-
sic provides general cortical arousal, as well as some specific
(priming) repetition of shared or overlapping circuits for mu
-
sic and spatial processing, which together may contribute to a
brief enhancement of spatial skills. Longer term exposure to
music, whether through extensive auditory exposure only (as
in the rat studies) or through extensive auditory exposure as
part of instrument practice, provides repeated and extended
cortical arousal and extensive repetition of the firing of
shared and overlapping neural circuits for music and spatial
skills. These extended effects, in turn, cause changes in gene
expression, and these changes in gene expression may lead to
reorganization of synaptic structures (and other forms of re
-
modeling of neural circuits). The structural changes may
support durative enhanced spatial skills.
This speculative model is consistent with neuroscience
findings and offers a coherent account of results from the dif
-
ferent types of music effect studies. It also provides an expla
-
nation for the fact that spatial skills are not the only cognitive
skills be found to be enhanced by music experience
(Schellenberg, 2004). Equally important, the model accounts
for spatial skill enhancement through music exposure or mu
-
sic instruction without invoking the unsupported notion of
transfer, and without resorting to a claim for a novel, previ
-
ously undiscovered cognitive process.
CONFLICTING CONSTRUCTS, FINDINGS,
AND CLAIMS FOR EMOTIONAL
INTELLIGENCE (EI)
Cherniss et al. (2006) argued that I was wrong to view multi-
ple conflicting EI measures and constructs as a problem,
wrong to argue that EI has limited predictive validity, wrong
to assert that Goleman claimed that EI accounts for more
than 80% of success, wrong to propose that EI was unlikely
to have a discrete neural system, and wrong to argue that EI
should not be applied in education. The following sections
address these five criticisms.
Lack of a Validated Unitary EI Construct
Remains a Problem
Cherniss et al. (2006) argued that the many conflicting EI
constructs are not a stumbling block for EI research. How
-
ever, the competing EI constructs demonstrate that EI is
poorly understood and make generalization across studies
extremely difficult. Van Rooy and Viswesvaran (2004) re
-
ported that studies of EI “have not used the same, or even a
few of the same, measures of EI” (p. 74). Moreover, efforts to
reconcile measures have been unsuccessful. For example,
Gignac, Palmer, Manocha, and Stough (2005) reported that a
confirmatory factor analysis could not even reconcile an off
-
spring measure of EI with its parent measure. Goldenberg,
Matheson, and Mantler (2006) could not demonstrate con
-
vergence of two measures of EI, the Mayer-Salovey-Caruso
Emotional Intelligence Test (MSCEIT) and SREIS, in a com
-
munity sample of 223 individuals. Correlations between
scores from the two EI measures for their three comparable
subscales (perceiving emotion, r = –.03; using emotions, r =
–.02; managing emotions, r = .04) were essentially zero
(Goldenberg, Matheson, & Mantler, 2006, p. 39).
Murphy (2006) reviewed the state of research on mea
-
sures of EI and concluded that not only are existing measures
INADEQUATE EVIDENCE 251
of EI inconsistent with one another but current constructs of
EI for which there are, as yet, no measures are so conceptu
-
ally unclear that these constructs will not be able to be trans
-
lated into measures.
EI Has Limited Predictive Validity
Cherniss et al. (2006) argued that, contrary to my review, five
published studies reported that EI has significant predictive
validity for a variety of life outcomes. However, these five
studies do not provide strong support for EI. One study as
-
sumed that attitudes, job skill, and leadership factors that dif
-
ferentiated better collection agents were subserved by EI
(Bachman, Stein, Campbell, & Sitarenios, 2000), and an
-
other reported only modest correlations for EI and leadership
(Rosete, & Ciarrochi, 2005). Lopes, Salovey, and Straus
(2003) expressed doubt about EI, concluding that “it is un
-
clear to what extent we are truly assessing skill, rather than
conformity or adjustment to social norms” (p. 655). Lopes,
Salovey, Côté, and Beers (2005) reported that only one of
four self-report EI subscales, emotional regulation, was asso
-
ciated with social adaptation (p. 5) and concluded that EI
skills “are likely to have only a modest impact on the quality
of social interactions” (p. 4). Moreover, the fifth study was a
meta-analysis of EI studies that revealed that EI did not have
predictive validity beyond that found for general intelligence,
but general intelligence did “significantly predict perfor-
mance beyond that explained by EI” (Van Rooy and
Viswesvaran, 2004, p. 87). Van Rooy and Viswesvaran
(2004) concluded that “the claims that EI can be a more im-
portant predictor than cognitive ability (e.g., Goleman, 1995)
are apparently more rhetoric than fact” (p. 87).
Van Rooy and Viswesvaran’s (2004) meta-analysis deter
-
mined that the correlation between EI and work performance
was .24 and between EI and academic performance was .10
(p. 86). Thus, EI predicted only 1% of the variance in aca
-
demic performance and only 8% of job performance vari
-
ance. Similarly, Bastian, Burns, and Nettelbeck (2005) re
-
ported that only 6% of the variance in life skills could be
predicted by EI (p. 1143).
Cherniss et al. (2006) cited Judge, Colbert, and Ilies
(2004) to argue that “IQ and other tests of cognitive ability
account for no more than about 25 percent of the variance in
outcomes.” However, Deary, Strand, Smith, and Fernandes
(2006) reported that intelligence scores predicted 48% of the
variance of performance on General Certificate of Secondary
Education exams, and Rindermann and Neubauer (2004)
similarly found that intelligence scores predicted 43% of the
variance in academic achievement. Schmidt and Hunter’s
(1998) meta-analysis found that general intelligence “g” is
the most valid predictor of job performance, and Gottfredson
(1997) reviewed meta-analyses of the predictive validity of
intelligence measures for job performance and reported a
range of predictive validity from 23% to 65%. Thus, contrary
to Cherniss et al.’s claim, studies have reported that general
intelligence accounts for more than 25% of the variance in
academic and job performance.
As noted by Cherniss et al. (2006), Van Rooy and
Viswesvaran (2004) found that EI had incremental predictive
validity in relation to personality factors (p. 86). However,
the EI basis for this increment is unclear, and the increment is
small. Gannon and Ranzijn (2005) found that EI added only
1.3% beyond the 34.2% of variance in life satisfaction ac
-
counted for by personality. Personality dimensions, in gen
-
eral, have been reported to have high predictive validity for
job performance. Hogan and Holland (2003), for example,
found that emotional stability predicted 43%, extraversion
35%, agreeableness 34%, conscientiousness 43%, and open
-
ness to experience 34% of variation in job performance.
No Ambiguity in Goleman’s Claim That EI
Accounts for More Than 80% of Success
Cherniss et al. (2006) offered no rebuttal of my claim that
Goleman’s 80% figure is a subjective judgment mistakenly
presented as “recent studies” (Waterhouse, 2006). Goleman
examined a list of 21 job skills that hegot from an unpublished
privately commissioned study (Goleman, 1998, p. 31) and de-
cided that 18 of the 21 skills were EI skills; thus, as 18 equals
85.7%of21,he judged that EI explainedmorethan80%oflife
success (Pool, 1997, p. 12) or more than 80% of job skill com-
petencies of superior workers (Goleman, 1998, p. 320).
In place of a direct rebuttal, Cherniss et al. (2006) sug-
gested that I had misunderstood the ambiguities in
Goleman’s work. However, Pool’s (1997) lecture report and
Goleman’s (1998) published statements are not ambiguous.
Pool did state that Goleman told members of the Associa-
tion for Supervision and Curriculum Development that “IQ
predicts only a small part of career performance—ranging
from 4 to 20 percent. But recent studies have shown that
emotional intelligence predicts about 80 percent of a per
-
son’s success in life” (p. 12). Goleman (1998) did claim
that “IQ alone at best leaves 75 percent of job success un
-
explained, and at worst 96 percent” (p. 19), and Goleman
(1998) did claim that “more than 80 percent of general
competencies that set apart superior from average perform
-
ers depend on emotional intelligence” (p. 320).
No Evidence for Neural Circuits for EI
Although at present no research has identified neural bases
for EI, Cherniss et al. (2006) argued that EI and IQ neural cir
-
cuits are separate, that EI depends on subcortical systems and
IQ on prefrontal cortex, and that EI includes discrete brain
systems for mindsight (recognizing that others have their
own thoughts) and for face recognition.
Cherniss et al.’s (2006) brain claims for EI ignore the fact
that behavioral studies have consistently reported significant
correlations between EI and IQ and between EI and personal
-
ity(Schulte, Ree, & Carretta, 2004; Van Rooy& Viswesvaran,
252
WATERHOUSE
2004). Consequently, theorizingabout the brain circuits for EI
shouldinclude consideration oftheevidencefor structural and
neurochemical brain bases for general intelligence (Shaw et
al., 2006) and for personality (Paris, 2005). Moreover, instead
of considering only mindsight and face recognition, specula
-
tive models should address the full range of existing evidence
for neural bases for EI component behaviors such as attach
-
ment, empathy, face and emotion recognition, emotional sen
-
sation, emotional expression, the mirror neuron system, lan
-
guage skills, personality components, working memory,
long-term memory, reasoning, decision making, and others
(Waterhouse, 2006).
EI Is Not a Basis for Moral Conduct
Cherniss et al. (2006) claimed that programs such as social
emotional learning (SEL) could be used to “enhance posi
-
tive youth development and mental health, reduce sub
-
stance use and antisocial behavior, and improve educational
outcomes.” However, because no one yet knows what EI
represents, beyond general mental ability and personality
components already identified as part of EI, and because
there is no empirically validated unitary construct of EI
(Murphy, 2006), therefore it remains premature to apply EI
to education. Furthermore, a review has suggested that
there is insufficient evidence for the beneficial effects of
SEL programs (Kristjannson, 2006).
Another problem of significance is that EI training has
been implied to be moral education. For example, Cherniss et
al. (2006) argued that EI/SEL training can reduce discipline
problems as well as make students more caring and responsi-
ble. However, in fact, nothing in any EI construct precludes
someone with high EI from being an immoral person.
Kristjannson (2006) analyzed whether or not components of
EI reflected moral principles, and he concluded that “EI lacks
moral depth and does not exclude the possibility that a calcu
-
lated Machiavellian personality can be deemed emotionally
intelligent” (p. 17).
In summary, none of Cherniss et al.’s (2006) five criti
-
cisms survived close examination. Researchers do not yet
know what the conflicting measures for EI are actually
measuring. The five studies published in academic journals
that Cherniss et al. outlined as evidence for EI did not pro
-
vide strong empirical support for EI, and one of the five, a
meta-analysis of EI studies (Van Rooy & Viswesvaran,
2004), found that EI predicted only 1% of the variance in
academic performance and only 8% of the variance in
workplace performance. Goleman did claim that EI pre
-
dicted 80% of life and work performance. No research has,
as yet, provided evidence for the possibility that there are
unique brain circuits for the two core domains of EI.
Finally, as EI components contain no moral principles, pro
-
ponents should desist from implying that EI school pro
-
grams can provide moral education.
CONCLUSION: PERSISTING WITHOUT
ADEQUATE EVIDENCE
Although Gardner and Moran (2006), Rauscher and Hinton
(2006), and Cherniss et al. (2006) claimed that there was a
wealth of empirical support for their theories, Gardner and
Moran offered no research evidence to validate MI, Rauscher
and Hinton included only three published music instruction
studies with significant positive findings for spatial skill en
-
hancement, and Cherniss et al. provided five published stud
-
ies whose findings did not provide strong support for the pre
-
dictive validity of EI.
Despite their inadequate empirical bases, these theories
have wide currency and, unfortunately, may continue to be
applied in education because they tell “good news” stories.
Gardner’s MI theory tells us the story that we each have
eight forms of intelligence, so there is likely to be one in
which we can shine. Rauscher’s music transfer theory of
-
fers spatial skill improvement through music lessons—a
cognitive bonus for keeping music in the curriculum.
Goleman’s EI theory tells the story that job and life success
depends much more on our EI than our IQ, with the good
news that we can increase our EI.
Tilly (2006) argued that there are four modes of explana-
tion: conventions (accepted reasons for events and actions),
stories (simple cause and effect accounts), codes (sets of
rules such as legal judgments), and technical accounts (sys-
tematic discipline-based empirical explanations). Gardner
and Moran (2006), Rauscher and Hinton (2006), and
Cherniss et al. (2006) argued that MI, the music instruction
effect, and EI were validated technical accounts of brain
systems. In the absence of adequate validating empirical
support, and in the absence of concord with neuroscience
findings, these three theories are not validated technical ac
-
counts. Therefore, at present, despite their appeal, they
should not be applied in education.
REFERENCES
Allix, N. M. (2000). The theory of multiple intelligences: A case of missing
cognitive matter. Australian Journal of Education, 44, 272–288.
Appleman, P. (Ed.). (2000). Darwin Third Edition. New York: Norton.
Astuti, R., Solomon, G. E., & Carey, S. (2004). Constraints on conceptual
development: A case study of the acquisition of folkbiological and
folksociological knowledge in Madagascar. Monographs for the Society
for Research in Child Development, 69(3), 1–135.
Bachman, J., Stein, S., Campbell, K., & Sitarenios, G. (2000). Emotional in
-
telligence in the collection of debt. International Journal of Selection and
Assessment, 8, 176–182.
Barnett, S. M., & Ceci, S. J. (2002). When and where do we apply what we
learn? A taxonomy for far transfer. Psychological Bulletin, 128, 612–637.
Bastian, V. A., Burns, N. R., & Nettelbeck, T. (2005). Emotional intelligence
predicts life skills, but not as well as personality and cognitive abilities.
Personality and Individual Differences, 39, 1135–1145.
Bowler, P. J. (1986). Theories of human evolution: A century of debate,
1844–1944. Baltimore: Johns Hopkins University Press.
INADEQUATE EVIDENCE
253
Cherniss, C., Extein, M., Goleman, D., & Weissberg, R. P. (2006). Emo
-
tional intelligence: What does the research really indicate? Educational
Psychologist, 41, 239–245.
Chikahisa, S., Sei, H., Morishima, M., Sano, A., Kitaoka, K., Nakaya, Y., et
al. (2006). Exposure to music in the perinatal period enhances learning
performance and alters BDNF/TrkB signaling in mice as adults. Behav
-
ioural Brain Research, 169, 312–319.
Costa-Giomi, E. (1999). The effects of three years of piano instruction on
children’s cognitive development. Journal of Research in Music Educa
-
tion, 47, 198–212.
Deary, I. J., Strand, S., Smith, P., & Fernandes, C. (in press). Intelligence and
educational achievement. Intelligence.
Deco, G., & Rolls, E. T. (2005). Attention, short-term memory, and action
selection: A unifying theory. Progress in Neurobiology, 76, 236–256.
Gannon, N., & Ranzijn, R. (2005). Does emotional intelligence predict
unique variance in life satisfaction beyond IQ and personality? Personal
-
ity and Individual Differences, 38, 1353–1364.
Gardner, H. (1983). Frames of mind: The theory of multiple intelligences.
New York: Basic Books.
Gardner, H. (1999). Intelligence reframed. New York: Basic Books.
Gardner, H. (2004). Audiences for the theory of multiple intelligences.
Teachers College Record, 106, 212–220.
Gardner, H., & Connell, M. (2000). Response to Nicholas Allix. Australian
Journal of Education, 44, 288–293.
Gardner, H., Feldman, D. H., & Krechevsky, M. (Eds.). (1998). Project Zero
frameworks for early childhood education: Volume 1, Building on chil
-
dren’s strengths: The experience of project spectrum. New York: Teachers
College Press.
Gardner, H., & Moran, S. (2006). The science in multiple intelligences:
A response to Lynn Waterhouse. Educational Psychologist, 41,
227–232.
Gignac, G. E., Palmer, B. R., Manocha, R., & Stough, C. (2005). An exami-
nation of the factor structure of the Schutte self-report emotional intelli-
gence (SSREI) scale via confirmatory factor analysis. Personality and In-
dividual Differences, 39, 1029–1042.
Goldenberg, I., Matheson, K., & Mantler, J. (2006). The assessment of emo-
tional intelligence: A comparison of performance-based and self-report
methodologies. Journal of Personality Assessment, 86, 33–45.
Goleman, D. (1995). Emotional intelligence. New York: Bantam.
Goleman, D. (1998). Working with emotional intelligence. New York: Ban
-
tam.
Goleman, D. (2001). Emotional intelligence: Issues in paradigm building. In
C. Cherniss & D. Goleman (Eds.), The emotionally intelligent workplace
(pp. 13–26). San Francisco: Jossey-Bass.
Gottfredson, L. S. (1997). Why g matters: The complexity of everyday life.
Intelligence, 24, 79–132.
Graziano, A. B., Peterson, M., & Shaw, G. L. (1999). Enhanced learning of
proportional math through music training and spatial-temporal training.
Neurological Research, 21, 139–152.
Green, L., Fein, D., Modahl, C., Feinstein, C., Waterhouse, L., & Morris, M.
(2001). Oxytocin and autistic disorder: Alterations in peptide forms. Bio
-
logical Psychiatry, 50, 609–613.
Hetland, L. (2000). Learning to make music enhances spatial reasoning.
Journal of Aesthetic Education, 34, 179–238.
Hogan, J., & Holland, B. (2003). Using theory to evaluate personality and
job-performance relations: A socioanalytic perspective.
Journal of Ap
-
plied Psychology, 88, 100–112.
Judge, T. A., Colbert, A. E., & Ilies, R. (2004). Intelligence and leadership:
A quantitative review and test of theoretical propositions. Journal of Ap
-
plied Psychology, 89, 542–552.
Kahneman, D. (2003). A perspective on judgment and choice: Mapping
bounded rationality. American Psychologist, 58, 697–720.
Kovas, Y., & Plomin, R. (in press). Generalist genes: Implications for the
cognitive sciences. Trends in Cognitive Science.
Kristjannson, K. (2006). “Emotional intelligence” in the classroom? An Ar
-
istotelian critique. Educational Theory, 56, 39–56.
Lieberman, P. (2002). On the nature and evolution of the neural bases of
human language. American Journal of Physical Anthropology, 235,
36–62.
Lopes, P. N., Salovey, P., Côté, S., & Beers, M. (2005). Emotion regulation
abilities and the quality of social interaction. Emotion, 5, 113–118.
Lopes, P. N., Salovey, P., & Straus, R. (2003). Emotional intelligence, per
-
sonality, and the perceived quality of social relationships. Personality and
Individual Differences, 35, 641–658.
Mayer, R. E. (2004). Teaching of subject matter. Annual Review of Psychol
-
ogy, 55, 715–744.
Modahl, C., Fein, D., Waterhouse, L., & Newton, N. (1992). Does oxytocin
deficiency mediate social deficits in autism? Journal of Autism and Devel
-
opmental Disorders, 22, 449–551.
Modahl, C., Green, L., Fein, D., Morris, M., Waterhouse, L., Feinstein, C, et
al. (1998). Plasma oxytocin levels in autistic children. Biological Psychia
-
try, 43, 270–277.
Murphy, K. (Ed.). (2006). Critique of emotional intelligence: What are the
problems and how can they be fixed? Hillsdale, NJ: Lawrence Erlbaum
Associates, Inc.
Oreskes, N. (Ed.). (2003). Plate tectonics: An insider’s history of the modern
theory of the Earth. Boulder, CO: Westview.
Paris, J. (2005). Neurobiological dimensional models of personality: A re
-
view of the models of Cloninger, Depue, and Siever. Journal of Personal
-
ity Disorders, 19, 156–170.
Perruchet, P., & Vinter, A. (2002). The self-organizing consciousness. Be
-
havioral and Brain Sciences, 25, 297–388.
Phelps, E. A. (2006). Emotion and cognition: Insights from studies of the hu
-
man amygdala. Annual Review of Psychology, 57, 27–53.
Pool, C. R. (1997). Up with emotional health. Educational Leadership, 54,
12–14.
Rauscher, F. H. (2002). Mozart and the mind: Factual and fictional effects of
musical enrichment. In J. Aronson (Ed.), Improving academic achieve-
ment: Impact of psychological factors on education (pp. 269–278). New
York: Academic.
Rauscher, F. H., & Hinton, S. C. (2006). The Mozart effect: Music listening
is not music instruction. Educational Psychologist, 41, 233–238.
Rauscher, F. H., Shaw, G. L., Levine, L .J., Wright, E. L., Dennis, W. R., &
Newcomb, R. (1997). Music training causes long-term enhancement of
preschool children’s spatial-temporal reasoning abilities. Neurological
Research, 19, 1–8.
Rauscher, F. H., & Zupan, M. A. (2000). Classroom keyboard instruction
improves kindergarten children’s spatial-temporal performance: A field
experiment. Early Childhood Research Quarterly, 15, 215–228.
Rindermann, H., & Neubauer, A. C. (2004). Processing speed, intelligence,
creativity, and school performance: Testing of causal hypotheses using
structural equation models. Intelligence, 32, 573–589.
Rosete, D., & Ciarrochi, J. (2005). Emotional intelligence and its relation
-
ship to workplace performance outcomes of leadership effectiveness.
Leadership and Organization Development Journal, 26, 388–399.
Schellenberg, E. G. (2003). Does exposure to music have beneficial side ef
-
fects? In I. Peretz & R. Zatorre (Eds.), The cognitive neuroscience of mu
-
sic (pp. 430–448). New York: Oxford University Press.
Schellenberg, E. G. (2004). Music lessons enhance IQ. Psychological Sci
-
ence, 15, 511–514.
Schmidt, F. L., & Hunter, J. E. (1998). The validity and utility of selection
methods in personnel psychology: Practical and theoretical implica
-
tions of 85 years of research findings. Psychological Bulletin, 124,
262–274.
Schulte, M. J., Ree, M. J., & Carretta, T. R. (2004). Emotional intelligence:
not much more than “g” and personality. Personality and Individual Dif
-
ferences, 37, 1059–1068.
Shaw, P., Greenstein, D., Lerch, J., Clasen, J., Lenroot, R., Gogtay, N., et al.
(2006). Intellectual ability and cortical development in children and ado
-
lescents. Nature, 440, 676–679.
Squire, L. R., & Kandel, E. R. (2000). Memory: From mind to molecules.
New York: Freeman.
254 WATERHOUSE
Tilly, C. (2006). Why? Princeton, NJ: Princeton University Press.
Trepel, C., Fox, C. R., & Poldrack, R. A. (2005). Prospect theory on the
brain? Toward a cognitive neuroscience of decision under risk. Cognitive
Brain Research, 23, 34–50.
Van Rooy, D. L., & Viswesvaran, C. (2004). Emotional intelligence: A
meta-analytic investigation of predictive validity and nomological net.
Journal of Vocational Behavior, 65, 1–95.
Waterhouse, L. (2006). Multiple intelligences, the Mozart effect, and emotional
intelligence: A critical review. Educational Psychologist, 41, 207–225.
Waterhouse, L., Fein, D., & Modahl, C. (1996). Neurofunctional mecha
-
nisms in autism. Psychological Review, 103, 457–489.
Wu, S., Jia, M., Ruan, Y., Liu, J., Guo, Y., Shuang, M., et al. (2005). Positive
association of the oxytocin receptor gene (OXTR) with autism in the Chi
-
nese Han population. Biological Psychiatry, 58, 74–77.
INADEQUATE EVIDENCE
255
