Methodologic
Standards
for Controlled
Clinical
Trials
of Early
Contact
and Maternal-Infant
Behavior
Mary
Ellen
Thomson,
MSc,
and Michael
S. Kramer,
MD
From the Departments of Epidemiology and Health and Pediatrics, McGill University Faculty of Medicine, Montreal
ABSTRACT. To provide an objective evaluation of
pub-lished studies on the effect of early contact on subsequent
maternal-infant behavior, a set of 1 1 methodologic
stand-ards generally applicable to controlled clinical trials of
perinatal care was developed. Sixteen reports of early
contact trials were assessed and seven of the 1 1 standards
were found to be satisfactorily fulfilled. The four
“prob-lem” standards were: adequate definition of subjects,
randomization, subject bias, and treatment
contamina-tion (care giver) bias. Of the five best trials fulfilling eight
or more ofthe standards, three reported a beneficial effect
of early contact, while two demonstrated no effect. The
evidence that early contact improves subsequent
mater-nal-infant behavior thus remains inconclusive. It is urged
that for future research in this domain more attention be
given to adequate subject definition, strict randomization
procedures, and safeguards against bias by the subjects
or their care givers. Pediatrics 1984;73:294-300; met
hodo-logic standards, controlled clinical triaLs, perinatal care,
maternal behavior.
most reporting positive results, ie, closer mother-infant ties. These results have contributed to public
pressure that has brought about significant changes
in obstetric care. Some physicians remain skeptical
on intuitive grounds, however, that a few minutes
of contact can have so lasting an outcome, and
some question the quality of scientific evidence
demonstrating benefits of early contact.’7”8
Rut-ter,’9 for example, concluded, “The findings are
important but the claims concerning a sensitive
period for maternal attachment rather outrun the
empirical evidence.”
To evaluate the evidence in an objective way, we developed a set of methodo!ogic standards for
din-ical trials of obstetric and neonatal care and then
applied these standards to the published reports of
early-contact trials.
DEVELOPMENT
OF STANDARDS
Does a brief period of contact between a mother
and her newborn at childbirth influence maternal
and infant behavior days, months, or years later?
A number of controlled clinical trials of early
con-tact have been published in the past decade,’’6
Received for publication Dec 28, 1982; accepted April 7, 1983. This is publication No. 84001 ofthe McGill University-Montreal Children’s Hospital Research Institute.
Presented in part at the annual meeting of the Ambulatory
Pediatric Association in Washington, DC, May 14, 1982.
Mrs Thomson is a recipient of a studentship award of the
Medical Research Council of Canada. Her current address is
3775 University St, Montreal, Quebec H3A 2B4, Canada.
Dr Kramer is a National Health research scholar of the National
Health Research and Development Program, Health and
Wel-fare Canada.
Reprint requests to (M.S.K.) Department of Epidemiology and
Health, McGill University Faculty of Medicine, 3775 University
St, Montreal, Quebec H3A 2B4, Canada.
PEDIATRICS (ISSN 0031 4005). Copyright © 1984 by the
American Academy of Pediatrics.
Based on the principles originally set out by
Hi!!,2#{176}amplified by recent literature,2129 and
mod-ified by our experience, 11 standards were
elabo-rated. We then tested these standards on trials of
perinatal care that did not involve early contact
and made appropriate modifications to arrive at the
final version. These 1 1 standards are categorized as
follows, according to Hill’s four stages of a clinical trial20: definition of the subjects (standard 1);
a!lo-cation of the subjects to treatment groups
(stand-ards 2 to 4); laying down of the treatment schedule
(standards 5 to 7); and measurement ofthe outcome
(standards 7 to 11).
Standard 1 applies to the adequate definition of
the subjects. Fulfillment of this standard requires
the establishment of selection criteria. These
cri-teria should be clearly stated in the report, and data
should be provided concerning the proportion of
Furthermore, if the participation rate (the
propor-tion of those meeting the selection criteria who
actually participated in the study) is low, the
inves-tigators should compare participants and
nonpar-ticipants in an attempt to show their comparability.
Standard 2 concerns the randomization or other
methods used for allocating subjects to the
treat-ments under study. In order to fulfil! this standard,
the author should not only mention that treatment
was assigned on a random basis, but also describe
the method of randomization. That method must,
to be truly randomized, lie outside the investigator’s
control.
Standard 3 concerns the verification that the
allocation of treatments yielded comparison groups
that were equivalent in all important respects, other
than the treatment under study. In other words,
have the researchers ensured that, ignoring possible
treatment effects, the groups are equally likely to
develop the outcomes under study? For studies
involving mothers’ behavior toward their infants, a
variety of clinical (parity, neonatal birth weight,
gestationa! age, and health status) and sociodemo-graphic (maternal age, ethnic origin, and
socioeco-nomic status) factors could affect the outcome. If
the treatment groups differ to an important extent
on one or more of these variables, stratification or
statistical adjustment should be performed when
the outcomes are analyzed. The adjusted results
should then be taken into account in drawing
con-clusions about the effects of treatment.
Standard 4 pertains to losses of subjects
occur-ring after the subjects are randomized or otherwise
allocated to treatment groups. The authors should
provide the reader with both the number of subjects
initially randomized and the number
subse-quent!y lost from a!! groups. Furthermore, if the
losses are substantial, lost subjects should be
com-pared (according to relevant base line variables and
treatment group) with those retained in the study.
If lost and retained subjects are not equivalent,
stratification or statistical adjustment again
be-comes necessary in analyzing the results.
The fifth standard concerns the definition of the
experimental and control treatments. Both should
be described in adequate detail, and it should be
clear that the treatments were defined before the
trial commenced-not “in progress” during the
course of the trial.
Standard 6 applies to possible contamination of
the treatment stemming from bias on the part of
the care givers. Investigators should provide and
report adequate safeguards to ensure that the
ex-perimenta! group does not receive any treatment,
beyond the maneuver under study, that is not also
received by the control group. Differential support
and encouragement by postpartum nursing staff is
an obvious example of the kind of treatment
con-tamination that could alter the results of a trial
concerned with maternal behavior.
Standard 7 applies to subject bias, ie, the
possi-bility that subjects’ awareness of their treatment
group assignments could influence the outcome
un-der study. This standard actually pertains to both
of Hill’s two latter stages, since subject bias can
affect either the treatment itself (a placebo effect)
or the measurement of the outcome (ie, the subject
behaves in a way she believes the researcher wants
or expects her to behave). Fulfillment ofthis
stand-ard requires that adequate safeguards be reported
for the design and conduct of the trial. Subjects in
the experimental group should be kept unaware of
any special status, and all subjects should be blind
to the research hypothesis.
The eighth standard relates to the reliability and
validity of the outcome measures used in the trial.
In particular, the investigators should take steps to
ensure that interobserver agreement is high among
research staff responsible for measuring the
out-come, or they should use single observers or
meth-ods not susceptible to subjective judgment. The
validity of measures in the domain of
maternal-infant interaction is often difficult to assess, but
when validated measures are available, they should
be used.
Standard 9 concerns the unbiased observation of
outcome. It is fulfilled by blinding the observers to
the treatment group assignment (experimental v
control) of all subjects under study.
Standard 10 pertains to the soundness of
statis-tical inferences made. In particular, the authors
should make clear what their hypotheses were prior
to the trial. Hypotheses generated by post hoc
analyses of the data should be treated as tentative.
Multiple testing should be accompanied either by
downward adjustment of the a level (the threshold
P value for inferring statistical significance) or by
cautious interpretation of the findings if the
cus-tomary a level (P
<
.05) is retained. Finally, so-called “trends” (usually reflecting differences asso-ciated with P>
.05) should not be overinterpreted.Finally, the eleventh standard relates to clinical
significance and statistical power. In a large trial,
trivia! differences may achieve statistical
signifi-cance without reaching a magnitude that has
din-ical relevance or importance. Conversely, small
trials may fail to produce statistically significant
differences merely because they lack the power to
detect small, but clinically meaningful, differences. Fulfillment of this final standard requires
consid-eration of these aspects of sample size in
METHOD
OF EVALUATION
We evaluated only trials published in refereed
journals that assessed the effect of extra contact
between mothers and term infants in the first few
hours and days after birth. Abstracts or accounts
given in books were thus excluded. We located 16
reports of 13 different trials. (The three extra
re-ports concerned two trials in which subsequent
follow-up studies measured longer-term outcomes
in the same subjects as the original trials.) We
emphasize that our evaluation concerned the
re-ports of trials, rather than the actual methods used
in the conduct of these trials, because it is the
reports that are generally available for
considera-tion and that serve as the basis for policy decisions.
Our aim was to evaluate the methodologic quality
ofthese trials, ie, the design, conduct, and reporting
of experiments that measured the effect of
treat-ments (early contact) on outcomes (certain
mater-nal-infant behaviors) chosen by the investigators;
we did not assess the appropriateness of the chosen
treatments and outcomes themselves. We thus did
not concern ourselves with such issues as the types
of mothers and infants; the nature, duration, and
timing of the contact; nor the short-term or
long-term importance of the behaviors studied. These
biologic-clinical issues have been critically reviewed
by Siegel.3#{176}
Criteria for fulfillment of the 11 methodologic
standards are contained in the “Appendix.” For four
of the 11 (standards 4, 6, 9, and 11), the criteria
were judged as either fulfilled or nonfu!fi!!ed. For
the remaining seven standards, partial fulfillment
resulted in assignment to an intermediate category.
We independently assessed each report by each
of the 1 1 standards. Agreement between the two
authors was high, with a weighted K score of +0.69.
(Weighted kappa is a statistical measure of
condor-dance between two observers that corrects for
TABLE. Consensus Ratings for 16 Reports
chance-expected agreement and allows for partial
agreement and disagreement. It ranges in value
from -1 to +1, with values above +0.5 representing
high levels of concordance.31) We then compared
and discussed our discrepant ratings, establishing a
consensus rating for each of the 1 1 standards on all
16 reports, and the consensus ratings were then
used to judge the fulfillment of the standards.
We calculated summary scores for each standard
to quantitate, in a rough way, the overall strengths
and weaknesses of the published reports by giving
half credit for partial fulfillment and expressing the
result as a percentage of the total possible score of 16:
Summary score
=
(no. of articles with standard fulfilled)
100 #{189}(no. of articles with standard partially fulfilled)
16 total articles
RESULTS
AND
DISCUSSION
The consensus ratings for each of the 16
pub-!ished reports on the 11 standards are shown in the
Table, along with the summary scores for each
standard. In genera!, the standards were we!!
fu!-filled, with seven of the 11 obtaining summary
scores of 69% to 100%. These seven standards will
receive no further discussion here; readers
inter-ested in pursuing the methodologic issues involved
are referred to several excellent reviews.2#{176} We
shall focus here instead on those standards
receiv-ing summary scores of 50% or less: Subject
defini-tion (standard 1), Randomization (standard 3),
Treatment contamination (standard 6), and
Sub-ject bias (standard 7).
The first problem standard was Subject
defini-tion. Although a majority of reports did mention
some selection criteria, few indicated the proportion
excluded. It was thus not clear whether the reported
findings apply to a!! women giving birth, to the
majority who give birth with no complications
Standard R efere nce N o. of Report Summary
Score (%)
1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16
-i-:-
Subject definition + #{247} + ± - + ± + ± ± ± 472. Randomization - - - - ± ± ± ± ± - ± - ± ± ± - 28
3. Equivalence of groups + + + + + - - + + + ± + + ± + + 81
4. Losses after randomization + + + + + + + + + + - + - + + + 87
5. Treatment definition + + + + + + + + + + + + + + + + 100
6. Treatment contamination - + + + + - - - + - - + - + + - 50
7. Subject bias + - - ± - - + + 22
8. Reliability/validity of outcome ± ± ± - + + + + + + - ± + + + + 75
meaures
9. Outcome observer bias - - - + + + + - + + + - + + + + 69
10. Statistical inferences + ± ± - + - - ± + + + + + + + + 72
11. Clinical significance and sta- + + + + + + + + + + + + + + - + 94
tistical power
whatever, or to some combination in between. We wonder also whether there were hidden selection
criteria, such as weekday, daytime deliveries. In
genera!, the subjects of these reports were poorly defined, as reflected by the summary score of 47%.
The second problem standard was
Randomiza-tion. The reviewed articles achieved a summary
score of only 28% on this standard. Half the articles
did not mention random assignment; only one
de-scribed the procedure used.
The crucial importance of the randomization
procedure in safeguarding the comparability
of the groups of patients has often been
empha-sized.20’22’3234 As Mainland2’ explains:
Experience has shown that the human being is an
ex-tremely poor instrument for the conduct of a random
selection. Whenever there is any scope for personal choice
or judgment on the part of the observer, bias is almost
certain to creep in. Nor is this a quality that can be
removed by conscious effort or training. Nearly every
human being has, as part of his psychological make-up,
a tendency away from true randomness in his choices.
Thus the method of randomization must be
care-fully planned and strictly executed so as to be
immune from the persona! choice or judgment of
the investigator. A random treatment order sealed
in opaque, consecutively numbered envelopes is a well-known example of such a method.
The third problem standard was Treatment
con-tamination. In these trials we were especially
con-cerned about the possible effect of care giver bias,
ie, the possibility that more interest,
encourage-ment, and support were given by the nurses,
phy-sicians, or others to the early-contact group. Few
of the reviewed reports mentioned any safeguards
against care giver bias, however, as reflected by the
summary score of 50% for this standard.
Although the “blinding” of care givers is a
corn-mon practice in trials of drugs, thereby effectively
eliminating care giver bias, such blinding is often
impossible in trials of health care. Obstetic care
trials are, in fact, particularly susceptible to
treat-ment contamination, because new mothers may be
especially sensitive to encouragement and support.
While it may be difficult to prevent care giver bias
entirely, some safeguards are necessary. For
exam-p!e, the time spent by nurses with mothers in both
groups could be equalized, or the members of the
hospital staff involved in the early-contact
treat-ment could be kept away from the mothers
there-after.
The fourth problem standard was Subject bias. Few of the reviewed reports mentioned any
safe-guards against subject bias; the summary score was
only 22%. We were particularly concerned about a
feeling of “specialness” among the mothers in the
experimental group, a feeling that might well affect
the outcome. Although the subjects of these trials
could not be blinded to their treatment, subject bias (like care giver bias) must be kept to a minimum
by thoughtful planning at the design stage of a trial.
One possible safeguard is to ensure that study
sub-jects remain unware that different treatments are
being compared. At the least, subjects should be kept unaware of the research hypothesis.
EVIDENCE
FOR
BENEFIT
OF EARLY
CONTACT
What can we conclude about the effectiveness of early contact? In the 16 reports evaluated, effec-tiveness was assessed by a variety of outcomes that could be loosely categorized as mothers’ behaviors toward their infants. The range and variety of these behaviors is extensive and includes maternal affec-tion (the number of times a mother looks at, talks to, smiles at, or touches her infant) at 36 hours after birth, breast-feeding at 6 to 12 weeks post partum, and parenting inadequacy during the first
18 months of life. Although indexes of infant
de-ve!opment, such as the Bayley Scales, were also
used in several studies, such infant outcomes were
not found to be affected. Thus the question under
debate is whether early contact affects a mother’s behavior toward her infant.
Of the 16 reports we reviewed, 13 concluded that extra contact in the first few hours and days after birth improved the measured maternal behaviors; three articles concluded that early contact was without effect. None of the reports, however, fu!-filled a!! 11 standards.
It is possible that the deficiencies noted are due
to poor reporting, rather than to flaws in the actual conduct of the trials. Evidence for such incomplete
reporting was found by Chalmers et a!,32 who wrote
to 59 authors who had omitted important
infor-mation in reports of their trials. According to the
responses, half the missing items had actually been
carried out. Thus it is probably safe to assume that
some trials are methodologically better than they
appear from their published reports. Nonetheless, evaluation of the evidence and policy decisions are
usually based on these reports, and readers should
be provided with the information necessary for
their evaluations and decisions.
We believe that the quality of trials, and not their
quantity, determines the validity of their
conclu-sions, if for no other reason than that positive trials
have a better chance of being published than
neg-ative ones. Such publication bias is particularly
likely with trials involving small numbers of
sub-jects, in which little importance can be attached to
negative results (owing to lack of power in the
majority reported trials of small sizes; ten of the 16 involved 50 or fewer subjects.
In comparing the quality of the reports, we found
that the positive reports tended to fulfil! fewer
standards (mean 7.0) than the negative reports
(mean 8.2), although this difference was not
statis-tica!ly significant. We then decided to focus on the
results of the trials of highest quality: the five trials
that fulfilled more than eight of the 11 standards.
Of these five trials, three concluded that extra
contact had a positive effect and two found that it
did not.
A number of reasons could be advanced to explain
the discrepancy in the results of the five best trials.
One possible explanation is a difference in the
control treatments, ie, the usual hospital routines.
In the three positive trials, control subjects only
briefly glimpsed at their infants immediately after
birth, whereas in the two negative trials, control
subjects held their infants (although wrapped) for
about five minutes. This difference in type and
duration of contact between the control mothers
and their infants could theoretically lead to
differ-ences in subsequent maternal behavior. This
hy-pothesis, however, remains to be tested.
Differences in the types of subjects studied, or in
the types of outcomes measured, reveal no evident
reasons for the inconsistent results. Trials in
simi-lar types of subjects produced both positive and
negative results; trials using the same outcome
mea-sure (maternal affectionate behavior at 36 hours
post partum) also yielded mixed findings.
We do not know which, if any, of these
consid-erations explains the conflicting results. Although five trials fulfilled more than eight of the standards,
none fulfilled all 11. We have argued for quality
rather than quantity of research reports. Thus, we
would place more credence in the findings of a few
studies fulfilling all of the standards rather than
base our conclusion on “majority rule.” It should be
emphasized, however, that no single study, even if
methodologically flawless, can guarantee the
dis-covery of truth. Besides the possibility of some
unforeseen source of bias, chance can and will
oc-casional!y lead to fallacious results. Thus
replica-tion by different investigators in different settings
using equally rigorous methods lends further
cre-dence to research findings.
The overall methodologic quality of clinical trials of early contact, although far from perfect, appears
comparable to that found in many trials of more conventional (“harder”) therapies in medical, pe-diatric, and obstetrical journals.33’35 Nonetheless,
our assessment of the evidence concerning the
ef-fect of early contact on mothers’ subsequent
behav-ior toward their infants reveals that the evidence
remains inconclusive.
RECOMMENDATIONS
FOR
FUTURE
RESEARCH
We suggest that future clinical trials in this
do-main give greater attention to the four areas that
have been, according to our evaluation, most
defi-cient in previous trials. Study subjects should be adequately defined, so that readers know to whom
the results apply and to whom they may be safely
extrapolated. Randomization should be strictly
ex-ecuted and we!! described. Finally, safeguards
should be provided against bias by either the
sub-jects or their care givers.
Although the randomized controlled trial is
gen-eral!y regarded as the most potent scientific too!
for the evaluation of medical treatments, the mere
use of this design does not in itself confer certainty on its conclusions. Some trials are methodologically
better than others, and confidence in the findings
of a given trial can be expected to rise directly with
the care that has gone into its planning and
exe-cution. With an outcome as emotionally-laden and
difficult to measure as the relationship between
mothers and their newborn infants, the
opportu-nities for bias are considerable, and the need for
methodologic rigor becomes even greater. The
cha!-lenge is great, but then so are the rewards.
ACKNOWLEDGMENTS
We acknowledge the helpful comments we received
from Professor James Hanley and Drs Tom Hutchinson
APPENDIX: Standards for Controlled Clinical Trials of Perinatal Care: Criteria for Fulfillment
Fulfillment Partial Fulfillment Nonfulfillment
1. Subject definition
a. States selection criteria a, but not b or c Selection criteria not provided
b. Provides proportion of population meeting cri-teria
c. If participation rate is low, compares partici-pants and nonparticipants.
2. Randomization
a. Mentions random assignment a, but not b Random assignment neither
men-b. Describes a method outside control of investi- tioned nor described
gator
3. Equivalence of groups
a. Checks for equivalence by comparing at least 7 Compares (and adjusts <4 of the 12 variables compared of the following 12 variables: age, parity, socio- for) 4-6 of the 12 vari- or, if different, satisfactory
adjust-economic status, race/ethnicity, marital status, ables ment not performed
type of delivery, method of feeding, health of the mother, gestational age, birth weight, sex, and health status of the infant
b. If important differences, performs stratifica-tion or other adjustment in analysis 4. Losses after randomization
a. Provides the numbers of subjects randomized Substantial losses neither
ac-and subsequent losses from groups counted for nor given cautious
in-b. If losses substantial, compares lost and re- terpretation
tamed subjects
c. If lost subjects different from those retained, performs stratification or other adjustment or interprets results cautiously
5. Treatment definition
a. Describes both experimental and control treat- Only experimental Experimental treatment not
ade-ments adequately treatment adequately quately described
b. Defines treatments prior to trial described (plus b)
OR
Evidence of change in treatment
schedule during course of trial 6. Treatment contamination
Care giving is identical in study and control Safeguards against treatment
con-groups, except for treatment under investigation tamination inadequately described
(ie, no contamination)
7. Subject bias
a. Experimental subjects unaware of special sta- b, but not a Safeguards against subject bias
in-tus adequately described
b. All subjects unaware of research hypothesis
8. Reliability/validity of outcome measures
a. Uses objective measures or single observer; if Reliability demon- Inadequate evidence or reliability
not, provides good evidence of interobserver strated for some mea- or validity of measures
agreement sures, but not all
b. Uses measures that are valid to best of current knowledge
9. Outcome observer bias
Observers blind to group assignment Blinding of observers not
men-tioned 10. Statistical inferences
a. Give primary importance to prior hypotheses a, but not b or c Firm inferences stated after post
and treats hypotheses generated by the data as hoc analysis or multiple testing
tentative (unless P < .001)
b. Adjusts P values when multiple outcomes are assessed or gives cautious interpretation
c. Does not overinterpret trends (P > .05)
1 1. Clinical significance and statistical power
a. Considers clinical significance if sample size is Clinical significance or power not
large and differences are small, yet statistically considered
significant
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