Journal of Pediatric Psychology, Vol. 27, No. 1, 2002, pp. 37-45
© 2002 Society of Pediatric Psychology
Methodological Issues in Outcome Studies of At-Risk Infants
School of Medicine, Southern Illinois University
All correspondence should be sent to Glen P. Aylward, SIU School of Medicine, Dept. of Pediatrics, P.O. Box 19658, Springfield, Illinois 62794-9658. E-mail: gaylward{at}siumed.edu .
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Abstract |
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Objective: To identify methodologic problems found in follow-up studies of infants at biologic and environmental risk and provide solutions and recommendations.
Methods: This article is a literature review.
Results: Problems fall into four groupings: (1) conceptualization/design issues, 2) subject population concerns, 3) procedural issues, and 4) measurement/outcome concerns.
Conclusions: Main-effect models are not useful; confounding and mediating variables must be identified. In addition, the following are needed: alternative analytic techniques, more precise subject selection and characterization of risk factors, geographically defined samples, broadened scope of outcome measures, and use of epidemiologic techniques.
Key words: developmental outcome; follow-up; high risk; infants; methodology.
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Introduction |
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Pediatric and clinical child psychologists are increasingly involved in follow-up of infants at biological and environmental risk (Aylward, 1997b
). This is due
in part to declining mortality rates and the resultant expanding numbers of
surviving infants at increased risk for developmental morbidity. In addition
to a focus on major disabilities (severe mental retardation, cerebral palsy,
sensory impairments, and epilepsy), interest has also focused on the
evaluation of more subtle, high prevalence/low severity dysfunctions:
learning, attention, and behavioral problems; borderline intelligence; poor
visual motor integration; deficits in spatial relations; reading and
mathematics problems; language disorders; and deficits in
"executive" behaviors.
Unfortunately, these follow-up studies often contain methodologic problems
that compromise findings. Approximately 10 years ago, we undertook a
meta-analysis of 80 follow-up studies published over the preceding decade
(Aylward, Pfeiffer, Wright, & Verhulst,
1989) and pooled results of 4,006 infants < 2500 g or smaller
and 1,568 controls. Eleven major problems were identified in these low
birthweight follow-up studies. Similar problems have been cited in more recent
reviews (McCormick, 1997a;
Tyson & Broyles, 1996)
with the inclusion of several recurrent issues: (1) use of gestational age
versus birthweight, (2) changes in test instruments, (3) use of
neuropsychological "batteries," (4) changes in medical procedures
(e.g., surfactant, steroids, ventilation), (5) application of sensitivity and
specificity measures, and (6) the need to include quality of life measures.
Comparability across studies is further reduced because of a lack of central
focus or framework for actual data collection due to the diversity of purposes
for follow-up (Johnson,
1997).
The following discussion highlights problems found in follow up of at-risk infants and contains suggestions for improvement. These problems fall into four broad areas: (1) conceptualization/design issues, (2) subject populations, (3) procedural issues, and (4) measurement/outcome.
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Conceptualization and Design Issues |
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Cause-Effect Inferences
In developmental follow-up studies, cause-effect inferences must be tempered by alternative explanations of observed effects that could be produced by confounding influences. Random assignment is not possible in studies of "naturally occurring" conditions such as extremely low birthweight (ELBW). In most follow-up studies, the predominant conceptualization of causal inference is (1) a condition (e.g., ELBW, drug exposure) leads to (2) some type of neurodevelopmental outcome. Unfortunately, this simplistic attribution of causality often is flawed on two ends.
First, multiple factors are associated with conditions such as ELBW
(McCormick, 1997a). These
include severity of neonatal course (days in hospital, other conditions),
sociodemographic factors (socio-economic status [SES] and social support,
race), subsequent illness (asthma, hospitalizations), maternal physical and
mental health, and environmental exposures to positive and negative
experiences (lead, smoking in household, intervention). In fact, some suggest
birthweight is best conceptualized as a marker of concomitant factors that
influence outcome. Second, at the outcome end there are neurodevelopmental,
cognitive, behavioral, health, and social issues. Various studies have shown
that front-end factors that influence outcome vary, depending on the time of
assessment, type of early risk factor, and type of outcome measured. In sum,
the situation is far more complex than a main-effect, "A
B"
model.
Spurious correlations may add much uncertainty to the model; this is
particularly concerning given that the data in most outcome studies are
correlational or descriptive. Depending on interpretation, Type I or Type II
errors could result. Inclusion of confounding variables will reduce the error
term and thereby decrease Type I errors. Moreover, measures selected to
represent potential confounds must be reliable and valid in and of themselves,
because measurement error in the control variables may detract from the
validity of any causal inferences that can be drawn
(Jacobson & Jacobson,
1996). When a perinatal variable and a potential confound such as
environmental risk are included in multivariate outcome analysis, a portion of
the variance will be attributed to the more reliable predictor solely because
it was measured more accurately. Conversely, even if a confounding variable
such as environment is very influential, if it is measured inaccurately, its
impact will be underestimated. In general, unreliable measurement at the front
end may produce Type II errors, whereas improper measurement of a confounding
outcome variable may increase variability and produce spurious correlations
(Type I error). Type II error is a particular problem when investigators fail
to detect subclinical behavioral or developmental deficits because of
insensitive test instruments.
This situation argues for use of measures with demonstrated reliability and
validity. Moreover, care must be taken to separate potential
confounding from mediating variables. Although both may
reduce the attributable influence of a particular perinatal variable on
outcome, interpretation of this influence depends on a priori categorization
of which variables theoretically are expected to function as mediators and
which as potential confounders; treatment of a mediator as a confounding
variable may lead to the incorrect inference of a spurious correlation or a
Type II error (e.g., Jacobson &
Jacobson, 1996). Both may be tested by adding a control variable
to the multivariate analysis. However, in the case of VLBW and environmental
influences, interpretation of a reduction in the effect of birthweight on some
outcome measure after environment is added depends on the hypothesized
function of this control variable (environment).
Selection of control variables should be determined both on a conceptual
basis and by univariate correlations that indicate at least a weak
relationship between the variable and the outcome measure of interest.
Multiple regression (stepwise and hierarchical) is often useful, but is
problematic when multicollinearity exists due to highly correlated predictor
variables, or when many correlated outcome variables are measured. Structural
equation modeling (interrelations among composite "latent"
variables are derived from multiple measures), partial least squares methods
(sometimes considered a variant of structural equation modeling; permits
detection of basic underlying patterns of association between constructs
[Carmichael-Olson, Streissguth, Bookstein,
Barr, & Sampson, 1994]), the use of LISREL in path analyses
(how well a hypothesized model fits the actual data), and growth curve
modeling are recognized techniques used to delineate more specifically the
role of confounding and mediating variables
(Keith, 1993;
Landry, Smith, Miller-Loncar, & Swank,
1997). Growth modeling is of particular interest: individual
differences in development are examined in terms of rate of change (slope) and
changes in the actual rate of change (curvature); this technique
could allow determination of whether mediating variables differentially affect
growth of cognitive or other abilities.
Control Groups
When inferences are made regarding the outcome of infants from an
identified group or those receiving a particular medical intervention, these
infants should be compared to some other group to make such inferences
meaningful (Kiely & Paneth,
1981). Traditionally, a full-term control group is used, drawn
from similar geographic and social circumstances. However, choice of the type
of comparison group depends on the purpose of the study and the hypotheses
being tested. For example, when considering the incidence of disability in
infants born at <800 g, use of a full-term comparison group would not be
very informative. A comparison group of infants with birthweights between 800
and 1000 g, drawn from the same population, would be more appropriate.
Determination of a control group when evaluating the efficacy of a new
procedure is more straightforward.
In the case of ELBW infants, within-group comparisons could be employed, based on arrays of medical/biologic pre- and perinatal factors, or contrasts between those who have done well on a particular outcome measure versus those who have not. Sample stratification can be used when a high degree of confound exists between a particular perinatal variable and one or more background variables. This has been successfully accomplished in studies where medical risk and biological risk are dichotomized (high/low), thereby yielding four possible stratifications. "Oversampling" of infants manifesting a condition under consideration that occurs less frequently (e.g., Grade IV intraventricular hemorrhage [IVH]), also assists in comparisons and decreases the possibility of Type II errors. Conversely, oversampling may be misleading if one were to consider the impact of the risk factor on the overall population.
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Subject Populations |
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Birthweight and Gestational Age
Prior to the 1990s, infants were primarily grouped by birthweight versus gestational age because of the uncertainty of the obstetric estimation of gestational age and the questionable utility of the postnatal assessment, particularly in very small infants (Hack & Fanaroff, 1988
). However, fetal ultrasound has improved
gestational age estimation, and gestational age is a stronger determinant of
organ/system maturation and viability than is birthweight. Moreover, infants
of very low birthweight may be (1) extremely premature babies (gestational
age) with AGA birthweights, (2) less premature babies with SGA (<3rd
percentile) birthweights, or (3) older pre-term and term infants with extreme
SGA birth weights (Touwen,
1986). This distinction is necessary because the ultimate survival
and outcome of infants included in these groups can vary markedly. Therefore,
both birthweight and gestational age should be considered in outcome
studies, with particular care taken to ensure that only AGA infants are
included in specific birthweight categories if this is the benchmark used for
grouping subjects.
Medical/Biologic Risk
More precise characterization of the neonatal medical experience or
biologic risk is necessary to compare outcomes across hospitals, for
benchmarking, and to control for population differences. Various risk scores
and neonatal admission severity scores for physiologic status and intensity of
therapeutic intervention have been developed (e.g.,
Pollack et al., 2000). These
scores may be used to stratify sub-groups or can be controlled statistically
in regression or ANCOVA analyses. Because the three major sources of morbidity
in the neonatal period are intracranial events, pulmonary immaturity, and
infections (McCormick, 1989),
severe ultrasound abnormality, septicemia, necrotizing enterocolitis, chronic
lung disease/bronchopulmonary dysplasia (BPD), hyperbilirubinemia, apnea of
prematurity, retinopathy of prematurity, and indicators of asphyxia, such as
seizures, should be included in the selected risk index. The number of days of
hospitalization after birth is often used as a marker variable; however, it is
disporportionately affected by smaller infants. If used, this variable should
be adjusted for birthweight or gestational age.
Medical/biologic variables fall into three broad areas: admission status (how "sick" the infant is, typically measured by variables such as birthweight, gestational age, Apgar score), medical response or intervention (ventilation, tertiary/secondary level of care), and sequelae at discharge (need for oxygen, neurosensory deficit, chronic illness). Each of these areas should be considered in follow up. Postdischarge medical status should also be noted, as subsequent hospitalizations are associated with lower verbal, visual-perceptual and visual motor scores, and less positive teacher ratings.
Sources of Bias
Samples. Small, single-hospital samples may yield data with
limited applicability because of the variations in routine medical care. For
example, the incidence of cerebral palsy can vary fourfold between different
neonatal intensive care units (NICUs), and outcomes may differ in terms of
whether the NICU is located in a hospital with a training program (marker for
teaching hospital) and the volume of babies admitted (proxy for experience)
(McCormick, 1997b). Although
use of control groups drawn from the same hospital population can minimize
this effect to some degree, pooling data from a geographically defined sample
is more appropriate. Geographically defined studies are sounder because the
numbers are larger, inferences are more secure, and hospital selection bias is
minimized. Regional data, or those derived from nationwide collaborative
networks, are most useful (Vermont-Oxford
Trials Network, 1993). The importance of proper selection of the
patient population cannot be underestimated, as the incidence of any outcome
strongly depends on the "denominator" (i.e., study population)
used (Escobar, Littenberg, & Petitti,
1991).
Age Cohort. The age cohort is important due to rapidly evolving
changes in medical interventions (Hack
& Fanaroff, 1999). For example, 30- to 40-year-old data on
asphyxia obtained from the National Perinatal Collaborative Study have
questionable relevance today. In terms of contemporary long-term follow-up, by
the time school-age data on a particular cohort are collected and analyzed,
practice changes in treatment may have occurred (e.g., assisted ventilation in
the delivery room, surfactant, and prenatal and postnatal steroids). This
argues for clear delineation of medical practices at the time of enrollment in
follow-up studies and timely data analyses.
Subject Loss. Subject loss can bias the estimation of rate of
handicap in follow-up studies (Tyson &
Broyles, 1996). Dropout rates as high as 40% to 50% have been
reported over the first year in indigent populations. Risk for dropout
increases in larger, less sick babies; those from lower SES households; babies
born to single, young mothers; and those not born at a tertiary care hospital.
Caretakers of infants with identified problems or disabilities are more
compliant with regard to follow-up attendance
(Aylward, Hatcher, Stripp, Gustafson, &
Leavitt, 1985; Campbell et
al., 1993), thereby potentially inflating rates of disability in
samples with a high dropout rate. Subject loss of 10% per year should be
anticipated, this arguing for power analyses to secure ample subject samples.
In addition, the convergent validity of other potentially useful data, such as
those provided by home health visitors, primary care physicians, and parent
report, should be explored as a means of reducing subject loss
(Johnson, 1997).
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Environmental Factors
The Hollingshead Index (1975
) was used in
approximately a third of the meta-analytic studies, whereas maternal education
was the most frequently used single marker variable. However, many children
are exposed to both biologic and environmental risk, and this combination is
sometimes referred to as "double jeopardy" or "double
hazard" (Escalona, 1982;
Parker, Greer, & Zuckerman,
1988). Here, nonoptimal biologic and environmental risks work
synergistically to affect later functioning (Aylward,
1990,
1992). However, there is a
ceiling effect in which a severe biologic risk will minimize environmental
influences. Stated differently, the sickest infants are least responsive to
environmental influences (Aylward,
1996; Bendersky & Lewis,
1994).
SES (maternal education and occupational status) is an insufficient marker
for environmental quality. Social support, which includes tangible components
(e.g., housing) and intangible components (attitudes, encouragement), should
also be considered. The environment involves both process (proximal
aspects experienced most directly; mother-infant interaction) and
status features (distal and broader, involving aspects experienced
more indirectly; social class; location of residence). Process or proximal
environmental variables are more predictive early on; status or distal factors
are more predictive later (Aylward,
1992). Environmental effects become increasingly apparent between
18 and 36 months, with 24 months cited frequently. Environmental variables
influence verbal and general cognitive outcome whereas medical/biologic
factors are more strongly related to neurologic and perceptual-performance
function (Aylward, 1996;
Bendersky & Lewis, 1994).
Medical/biologic factors tend to determine whether a developmental problem
occurs, but environmental factors temper or exacerbate the degree of problem
(Hunt, Cooper, & Tooley,
1988).
Negative components of the environment have a synergistic or additive
effect on infants who are biologically vulnerable
vis-à-vis the transactional
(Sameroff & Chandler,
1975) or "risk-route" models
(Aylward & Kenny, 1979).
Procedurally, infants can be stratified on some environmental measure (e.g.,
by quartiles), or environmental effects can be partialled out in statistical
procedures. If possible, process and status aspects need to be measured.
Because of the changing complexity and composition of contemporary
environments, valid, more recently developed measures comparable across
studies and administered quickly should be employed (see Aylward, 1997).
Correction for Prematurity
The consensus is that correction for prematurity should occur, arguably up
to 2 years of age (Hunt & Rhodes,
1977). However, some investigators suggest that correction not be
utilized or that that it be applied in an incremental fashion (e.g., half
correction), depending on the infant's gestational age, age at time of
measurement, and area of function being assessed
(Blasko, 1989); Miller,
Debowitz, & Palmer, 1984). Arguments for incremental correction currently
are not convincing. Imprecise gestational age estimation, concomitant medical
issues, and a lack of consensus whether to correct to 37 or 40 weeks are
additional confounds. Until a "correction algorithm" is devised,
correction through 2 years is recommended.
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Measurement/Outcome |
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Selection of Outcome Measures
Because there is no true "gold standard" in developmental assessment, terms such as "sensitivity" and "specificity" are misapplied. Instead, "co-positivity" and "co-negativity" are more appropriate in situations where scores on one test are compared to those obtained on a reference standard. The Bayley Scales of Infant Development (BSID; Bayley, 1969
) and the more
recent BSID-II (Bayley, 1993)
are traditionally considered the best criterion measures. However, analogous
to changes in medical procedures having an effect on outcome studies, changes
in outcome measures have a similar effect by limiting comparisons. Mean IQ/DQ
scores on a given test are estimated to increase 3 to 5 points per decade
(Flynn, 1999). Therefore, the
mean score of a test developed three decades ago conceivably could increase by
as much as 15 points. Such adjustments must be considered when comparing
scores in different age cohorts or longitudinally with different versions of
the same test, because change could be due to real improvement or be an
artifact of the different properties of the two instruments. Therefore, use of
outdated tests such as the Stanford-Binet Form LM in current protocols, is not
appropriate, nor is it useful to compare this with the more contemporary
version of the same test.
Additional controversy surrounds the BSID-II itself
(Gauthier, Bauer, Messinger, &
Closius, 1999; Matula, Gyurke,
& Aylward, 1997; Ross
& Lawson, 1997;
Washington, Scott, Johnson, Wendel, &
Hay, 1998). If corrected age is used to determine the beginning
item set, scores tend to be lower because the child is not automatically given
credit for passing the earlier item set. The potential to generate several
alternative developmental index scores may limit comparability across studies
that use BSID-II scores in research protocols.
Length/Duration of Follow-Up
A minimum of at least 3 years' follow-up appears necessary to identify
problems of moderate severity and to measure IQ. However, subtler, high
prevalence, low severity learning difficulties may not become apparent until
later, making follow-up into early school age the most desirable practice.
School entry is also an attractive end point because health and other problems
can be better defined at this age
(McCormick, 1989;
Vohr & Msall, 1997). If
the end point of follow-up is in itself a time of significant change and
variability (such as 12 months of age), outcome measurement might be further
compromised (e.g., the child who walks at 15 versus 12 months). In such
situations, it is difficult to separate a delay, disorder, or
deficit.
Selection of Outcomes
Traditionally, major handicaps were the primary focus in outcome studies.
Interest then shifted toward more subtle learning, attention, and behavioral
dysfunctions, and borderline IQ. Most recently, there has been a major
emphasis on a broader, multi-dimensional conceptualization of outcome and
health, including functional abilities, health status, and health-related
quality of life (HRQL; McCormick,
1989,
1997a;
Saigal et al., 1996). Children
at early biologic risk subsequently have poorer health (e.g., bronchopulmonary
dysplasia), related restrictions in ability to engage in usual childhood
activities, slower physical growth, and poorer social-emotional
development—all of which are not "traditional" morbidity
measures yet translate into compromised school performance and other sequelae.
As mentioned previously, documenting the child's health postdischarge is also
critical (Tyson & Broyles,
1996).
To evaluate outcome more precisely, in addition to
"traditional" measures, profiles of the following areas need to be
documented: health status; physical issues/limitations due to health;
functional status or quality of life including adaptive behavior and
day-to-day living; behavioral problems; social competency; gross, fine, and
visual motor skills; and academics. Emphasis on functional measures is
relatively new, due in part to difficulty in defining and measuring functional
limitations and then relating these limitations to performance status at
school, home, and the community (Msall,
DiGaudio, & Duffy, 1993). However, during infancy and early
childhood, parents must act as a proxy for the child, thereby increasing the
possibility of bias (Hack,
1999).
As a result, issue-specific outcome measures should be folded into a basic
outcome framework that could be compared across studies. This basic framework
should include a follow-up protocol with standardized age at assessment, areas
covered, and techniques used. However, more study-specific, narrow-band foci
could also be employed. This approach would allow for investigation of
specific deficits pertinent to the purpose of the follow-up study in
conjunction with more "standard" cognitive, behavioral/social,
functional, and health-related outcomes that would be of interest across
studies (e.g., Taylor, Klein,
Schatschneider, & Hack, 1998). The challenge is to accomplish
this in a reasonable amount of time and at an acceptable cost.
Outcome Analyses
The correlation coefficient often is used in descriptive investigations
relating perinatal variables and outcomes, or between two developmental scores
obtained at different times. Unfortunately, this statistic is subject to the
problem of restriction of range, where a fairly homogeneous distribution of
scores can produce a low correlation. Moreover, correlations do not provide
information regarding individual developmental patterns. Siegel
(1985) emphasizes the need to
predict ranges of scores, rather than exact scores.
Correlations are misleading in that regard, as they assume a level of
measurement precision not achieved in psychologic tests, environmental
measures, or biomedical variables. Additionally, if risk factors and outcomes
have differing distributions, an artificial cap may be placed on correlations
and variance.
Because group means may mask individual patterns of cognitive development,
and biologic risk groups are heterogeneous in terms of biomedical and
sociodemographic variables, cluster analysis is attractive
(Koller, Lawson, Rose, Wallace, &
McCarton, 1997; Liau & Brooks-Gunn, 1993). This technique
allows identification of homogeneous subsets of children with similar
developmental patterns. These clusters of infants could be compared on
variables "internal" to the cluster (e.g., risk or cognitive
scores); variables "external" to the clusters (biomedical and
sociodemographic) could be compared across clusters
(Koller et al., 1997). This
type of analysis has been used for cognitive development and holds promise
with neuromotor, functional, and health outcomes as well.
Other useful outcome analyses relating to measures of effect are derived
from developmental epidemiologic studies
(Scott, Mason, & Chapman,
1999). Here, the interest is on differences in
proportions of cases rather than differences in means or variance
accounted for. This approach yields qualitatively different information about
relationships among risk factors and developmental outcomes than is obtained
through more traditional analyses. The risk-ratio, typically used in
prospective, longitudinal cohorts, reflects the relative increase in the
probability of a negative outcome when the infant experienced a risk condition
(e.g., ELBW with IVH versus ELBW without IVH, compared in terms of spastic
diplegia). Effect of a risk factor (ELBW and IVH) is compared to some other
referent group (ELBW).
The odds ratio is typically used in casecontrolled retrospective
studies in which infants are chosen based on whether they exhibit the outcome
of interest (spastic diplegia), and data are gathered regarding previous
exposure to a risk factor (IVH). The ratio is the increased odds of a negative
outcome in infants who experienced a risk factor, relative to those who did
not experience the risk factor. This is particularly useful when a condition
is relatively rare (e.g., Grade IV IVH). Logistic regression could be employed
in this analysis. Both of these techniques are sometimes considered
"relative risk," although this is not universally endorsed; if the
incidence of an outcome is rare (<2%), the risk and odds ratio values
become similar (Scott et al.,
1999). These measures of effect are inherently different from
regression/ANOVA models, as small differences in means between two groups can
nonetheless lead to a larger difference in the proportion of extreme
cases in these groups (i.e., a factor associated with a small mean decrease in
IQ nonetheless may account for a larger number of children with mental
retardation).
Receiver operating characteristic (ROC) curves can provide a qualitative
measure of a test's diagnostic performance
(Centor & Schwartz, 1985)
or the accuracy of a variable or grouping of variables in predicting outcome.
Here the true-positive ratio rate is plotted against the false-positive rate
for different threshold values. Points along the diagonal line indicate an
equal chance of positive/negative outcome; the higher the ROC curve is from
this line, the better the prediction. The area under the curve (AUC) is a
quantitative measure of this discrimination, ranging from.5 (chance) to 1.0
(perfect discrimination). This technique has only recently been used in
developmental outcome studies (Pollack et
al., 2000).
Effect sizes need to be reported in outcome studies, as a small p
value does not necessarily imply an important finding—it simply
indicates the null hypothesis is not true
(McCartney & Rosenthal,
2000). Traditional p values should be accompanied by
estimates of both the size and direction of an effect. Two types of effect
size estimates exist: r Family (assessed via correlation) and d
Family (comparison of group means). Both are applicable in outcome
studies and are more practically useful than binary decisions based on
significance/nonsignificance. Effect sizes can be biased by measurement error,
methodological choices (e.g., within- versus between-subjects designs) or by
minimizing error terms (see McCartney
& Rosenthal, 2000).
Criteria
There is a lack of consistency in terms of diagnostic criteria. Arguments
are made both for and against viewing data as categorical or continuous. For
example, in the meta-analysis of LBW studies, had a binary "normal/not
normal" categorization been employed, no group differences would have
been detected. However, viewing the data in a continuous fashion yielded a
6-point difference between LBW and control infants. It would appear that
analyses of continuous data require decisions to include or delete severely
involved infants; either option would alter results. Use of categorical
methods allows inclusion of these babies but masks more subtle findings. Floor
effects and missing data are particularly problematic. "Outliers"
whose raw scores cannot be converted into scaled scores (as in the case of a
BSID-II score <50) often are "censored" or excluded, and a high
frequency of censoring may occur in populations with severely affected
infants. As a solution, imputed values may be used (e.g., a score of 49 is
recorded to indicate an unscalable score) and data analyzed using standard
methods (see Lindsey, O'Donnell, &
Brouwers, 2000). Means, corrected for censoring, can be compared
to means based on inclusion of imputed values to verify that imputation is
appropriate. With the BSID-II, extrapolated raw scores may be considered as an
alternative (see Black & Matula,
2000). It is recommended that the mean IQ (and SD) and effect
sizes and confidence intervals for each group, the proportion of mental
retardation and borderline intelligence, and the proportion of major disorders
(CP, blind, deaf) be reported. Comparisons excluding children with major
handicaps provide insight as to how children who survive without major
handicap fare.
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A promising area of research includes relating routine brain imaging techniques, such as cranial ultrasound, and less frequently employed techniques, such as cerebral blood flow (PET or SPECT), oxygen or glucose metabolism (PET), and functional activity of the brain (echoplanar or FMRI), to outcomes. Use of biochemical markers such as pro-inflammatory cytokines and protective oligotrophins and neurotrophins (Dammann & Leviton, 1999
)
may enhance predictive accuracy in outcome studies. These investigations will
require expanded collaboration among pediatric psychologists and other
disciplines. It appears that a national consensus is needed with regard to
elements and procedures necessary in basic follow-up protocols, to allow
comparability across studies and pooling of data. In summary, those involved
in developmental follow-up must realize that their data will influence
actual decisions made for real children; it is imperative
that these data be accurate and based on sound methodology. |
Acknowledgments |
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Special thanks to Steven J. Verhulst for his helpful manuscript review.
Received December 1, 1999; revision received July 1, 2000; accepted October 1, 2000
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References |
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