Inappropriate use of randomised trials to evaluate complex phenomena: case study of vaginal breech deliveryBMJ 2004; 329 doi: https://doi.org/10.1136/bmj.329.7473.1039 (Published 28 October 2004) Cite this as: BMJ 2004;329:1039
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Another reason why randomised controlled trials do not necessarily tell the whole truth in clinical medicine
The randomised controlled trial (RCT) is considered to be the gold
standard (or at least the silver standard, Simon, 2001) in clinical
research and by far superior to all other forms of study design. There
are good reasons to accept this. Non-randomised trials may generate all
kinds of bias. Observed outcomes may be caused by differences among the
patients given the two treatments, rather than the treatments alone
(Barton, 2000). The only way to avoid known differences (selection bias)
as well as concealed differences (confounding bias) between treatment and
control groups, is to let fate determine to which group a given patient
will be allocated (Grimes and Schultz, 2002). Blinding furthermore
precludes information bias. One can expect that, if the sample size is
large enough, the play of chance will conduct to similar groups, in which
possible confounding factors are equally distributed. Any result in
outcome may then be attributed to the intervention under study. If no
significant differences in outcome are detected, either the intervention
is not effective, or the power of the trial is not sufficiently large to
detect a real difference. Of course, in the latter case one may question
the clinical relevance of a possible small difference.
Some limitations of the RCT have recently been demonstrated by
Kotaska (2004) who showed that in heterogeneous populations and for
complex phenomena the conclusions of a RCT may not necessarily be valid
for each individual patient.
In this letter, we want to further argue that the RCT indeed has this
limitation, which has to be kept in mind by readers of medical literature.
Besides recognised restrictions concerning the external validity and other
forms of bias, we will also dispute the internal validity of the RCT, with
respect to patient subgroups. A few examples will demonstrate that the
conclusions of RCT 's may not be valid for every patient and therapies
should not be a priori rejected because they are not proven efficacious.
One of the recognised problems of the RCT is its limited external
validity. It may not always be possible to generalise its results to the
broader community, because screened volunteers for RCT 's are often good
prognosis patients, in contrast to the general population (Grimes and
Schultz, 2002). In the recent years two papers challenged the concept of
the superiority of the RCT over well-designed observational studies
(Benson and Hartz, 2000; Concato et al., 2000), and one of the arguments
they used to explain their conclusion, was the limited external validity
of RCT 's, in contrast with observational studies.
Although the RCT undoubtedly remains a very powerful tool to study
possible effects of a treatment, its conclusions are often used in an
incorrect way, for instance because of exaggerated enthusiasm for a
positive result, or the tendency of clinicians to overestimate benefit and
underestimate harm. The dangers of interpretation bias and dissemination
bias of the results of RCT 's have been convincingly exposed by McCormack
and Greenhalgh (2000), using the 'United Kingdom prospective diabetes
study' as an example. In day-to-day practice, clinicians who try to
follow the principles of evidence-based medicine are at risk for only
accepting and applying treatments that have been validated by RCT 's, and
rejecting therapies the efficiency of which has not been proven by a RCT.
In contrast to the problem of limited external validity, the internal
validity of the RCT usually goes unquestioned because of the design of the
RCT. This design follows the rules of controlled experiments in basic
science. In basic science, however, experiments are usually performed on
subjects (cell cultures or laboratory animals) that are behaving in a
predictable and identical way. Human beings usually do not behave in an
identical and predictable way. The RCT design assumes that all
interventions are effective (or not) to the same extent for all patients,
who should all behave in the same way, since they have been properly
randomised. Just like meta-analysis suffers from heterogeneity between
studies, RCT 's suffer from (often concealed) heterogeneity between
patients. The inference of a properly designed RCT is that a certain
intervention is more, less or as effective as another, for an average
population of patients. It actually does not tell anything about a given
individual patient. Stephen Jay Gould, a Harvard evolutionary biologist,
has nicely elaborated on this in his text “The Median Isn't the Message”
(http://www.cancerguide.org/median_not_msg.html), dealing with his own
survival prognosis after he received a fatal cancer diagnosis.
In reproductive medicine the main outcome of many trials is
pregnancy, and it is easily acknowledged that the successful establishment
of a pregnancy is a complex and multifactorial process. Even in
controlled assisted reproductive technology (ART) trials, establishment of
pregnancy still is determined by many factors, such as oocyte quality,
post-fertilisation embryonic events that are not quite understood (Tucker,
1990), and implantation (Denker, 1993; Lessey, 2000). Some therapeutic
trials may affect the outcome of àll patients in one way or another, e.g.
trials comparing stimulation protocols, because the outcome of the
treatment strongly correlates with the number of oocytes obtained. But
some interventions, in which pregnancy is the main outcome measure, may be
effective for some patients, but not for others, and a randomised trial
will not allow to detect this.
Many clinicians feel that interventions, that have not been proven
overall effective in a RCT, must be avoided. We believe this can be
wrong in some instances, because interventions may work for only certain
subgroups of patients and if these minority subgroups are not identified
before the trial starts (and they can not be identified because they are
unknown), it is impossible to detect this effect. In reproductive
medicine there are many examples of treatments considered to be
controversial, because some trials do not demonstrate an effect whereas
other (often smaller) trials do. How to interpret these results? Wait
for a meta-analysis? This will not solve the problem. We will try to
demonstrate that it is impossible to prove the efficacy of a treatment, if
it does not work for the majority of patients, but only for a subgroup, or
vice versa. We will consider two opposite situations. In the first
scenario a new treatment is tested that is beneficial for a subgroup of
patients, but has no effect whatsoever for the other patients. Scenario 2
is a situation in which a new treatment is beneficial for most patients
but not for a subgroup.
Scenario 1: Take two groups of 1000 patients each, who undergo a new
therapeutic intervention and a placebo treatment, respectively. Assume
that in both groups 90% of the patients are standard patients for whom the
new treatment will make no difference, because they are good prognosis
patients (G-patients). Both groups therefore contain a minority of 10%
bad prognosis patients (B-patients), who will benefit from the new
treatment. The proportion of G-patients and B-patients in each group
should be the same, thanks to the randomisation process. Pregnancy rate
for G-patients is 40% in the treatment group as well as in the control
group. The pregnancy rate for the B-patients, however, increases from 10%
in the control group to 40% in the treatment group. Table 1 shows the
statistics of this scenario. It is clear that the conclusion of the trial
will be that there is no significant difference in pregnancy rates between
the two groups (37% and 40% respectively). The relative risk (RR) is 1.05
(95% confidence interval or CI : 0.98-1.12). In the subgroup of B-
patients, however, the pregnancy rate increases from 10% to 40%, yielding
a RR of 1.50 (95% CI: 1.26-1.78), which is highly significant
(P<_0.0001. because="because" of="of" the="the" dilution="dilution" this="this" group="group" patients="patients" for="for" whom="whom" treatment="treatment" works="works" in="in" total="total" population="population" effect="effect" is="is" not="not" detected="detected" and="and" rejected.="rejected." wrongly="wrongly" so="so" bad="bad" prognosis="prognosis" p="p"/> Scenario 2: Two groups of 1000 patients undergo a treatment that is
beneficial for the G-patients (the pregnancy rate increases from 30% to
50%), but not for the minority of B-patients (the pregnancy rate is 10%
and remains 10%). Table 2 depicts this situation. Now, the difference
for the G-patients is significant (RR 1.67; 95%CI 1.48-1.88), as well as
in the total group (RR 1.64; 95%CI 1.46-1.85). The trial fails to detect
that there is a subgroup of patients for whom the treatment does not work
and we wrongly conclude that it may work in all instances…
Of course, many other scenarios are possible. We can vary the
proportion of good and bad prognosis patients (but they will remain the
same between groups, because of the randomisation process). We can
analyse much more subgroups of patients with intermediate prognoses, or we
can think of treatments that are beneficial for one group of patients but
harmful to others… It is clear from this exercise that RCT 's only tell
part of the truth, since they do not account for this effect.
Absence of a significant difference between treatments and controls
in a RCT does not mean that treatment and control are equivalent ("lack of
evidence of a difference does not mean that there is evidence of a lack of
difference", (Altman and Bland, 1995). In the same way, absence of
significant differences between treatments and controls do not rule out
that the treatment be beneficial in certain subgroups. This means that
therapies which are not “proven” to be efficacious should not a priori be
rejected for all patients. In the same way conclusions from positive
studies should not always be accepted and implemented in all instances.
Indeed, patient heterogeneity is not only a problem in negative studies,
but also in positive studies… It is important, however, to realize that
the RCT in this is not to blame, but our lack of knowledge how to identify
possible subgroups of patients and when to apply the conclusions of the
In order to identify a possible subgroup of patients, for whom an
otherwise ineffective treatment may be effective (or vice versa), one can
apply discriminant analysis or some other multivariate statistical
technique to all known entry variables, and look for discriminators which
distinguish responders from non-responders. When these discriminators
have been identified, a second, independent randomised trial may be
performed, stratifying for the distinguished features. If there is a
responsive subgroup, their stratum will show a greater response and the
subgroup will have been identified.
Another solution is to wait for new techniques which will enable
proper subgroup identification. A good example of this is the discovery
of polymorphisms in cytochrome p450 genes, which account for differences
between individuals in cancer risk and also in risk for adverse drug
reactions (this is the subject of pharmacogenomics, Tribut et al., 2002).
Another example is the subtypes of leukaemia which have been identified
using microarray cell type analysis and which strongly correlate with
prognosis (Stevenson et al., 2001). New techniques may thus lead to
subgroup identifications which were not possible before. Concerning
reproductive medicine, however, many of the patient characteristics which
we may need to identify the subgroup, are lacking or simply unknown, due
to our limited knowledge about all factors that lead to pregnancy.
There are quite some examples in reproductive medicine illustrating
the problem of subgroup identification. Assisted hatching is definitely
not beneficial for all patients undergoing ART (Hellebaut et al., 1996),
but maybe it is in a subgroup? Our RCT on assisted hatching of 1996
illustrates the hypothesis of subgroup effectiveness. We obtained a
pregnancy rate of 42.1% in the assisted hatching group and 38.1% in the
control group. These figures nicely fit the figures of Table 1, which
could mean that there indeed is a subgroup for which assisted hatching
would be beneficial. We are eagerly awaiting the results of the ongoing
Cochrane review on this subject (Seif et al., 2002).
Another example is the often controversial and non-validated
treatment for unexplained and repetitive implantation failure after ART.
Many therapies have been offered to these patients: zygote intrafallopian
transfer (Levran et al., 2002), autologous endometrial coculture
(Spandorfer et al., 2002), intravenous immunoglobulins (Coulam et al.,
2000), cytoplasmic transfer (Barritt et al., 2001), blastocyst transfer
(Simon and Pellicer, 2000) and many other. The large number of therapies
offered to patients suffering from unexplained recurrent miscarriage is
another well known example (aspirin, heparin, intravenous immunoglobulins
(Bracnch et al., 2001), leukocyte immunotherapy (Clark et al., 2001), for
further review see Kutteh (1999) and Lee and Silver (2000). Both
unexplained implantation failure after ART and unexplained recurrent
abortion leave us with a sense of helplessness, and in front of the
patient imploring us to do something, many clinicians will offer
controversial and unproven therapies. Believers of evidence based
medicine will reject most of these, but we believe that evidence itself
shows that the truth often remains covert.
Altman DG and Bland JM (1995) Absence of evidence is not evidence of
absence. BMJ 311, 485.
Barritt J, Willadsen S, Brenner C and Cohen J (2001) Cytoplasmic
transfer in assisted reproduction. Hum Reprod 7, 428-435.
Barton S (2000) Which clinical studies provide the best evidence?
BMJ 321: 255-256.
Benson K and Hartz AJ (2000) A comparison of observational studies
and randomized, controlled trials. N Engl J Med 342, 1878-1886.
Branch DW, Porter TF, Paidas MJ, Belfort MA and Gonik B (2001)
Obstetric uses of intravenous immunoglobulin: successes, failures, and
promises. J Allergy Clin Immunol 108 (4 Suppl): S133-138.
Clark DA, Coulam CB, Daya S and Chaouat G (2001) Unexplained sporadic
and recurrent miscarrage in the new millennium: a critical analysis of
immune mechanisms and treatments. Hum Reprod Update 7, 501-511.
Concato J, Shah N and Horwitz RI (2000) Randomized, controlled
trials, observational studies, and the hierarchy of research designs. N
Engl J Med 342, 1887-1892.
Coulam CB and Goodman CC (2000) Increased pregnancy rates after
IVF/ET with intravenous immunoglobulin treatment in women with elevated
circulating C56+ cells. Early Pregnancy 4, 90-98.
Denker HW (1993) Implantation: a cell biological paradox. J Exp Zool
Grimes DA and Schulz KF (2002) An overview of clinical research: the
lay of the land. The Lancet 359, 57-61.
Hellebaut S, De Sutter P, Dozortsev D, Onghena A, Qian C and Dhont M
(1996) Does assisted hatching improve implantation rates after in vitro
fertilization or intracytoplasmic sperm injection in all patients? A
prospective randomized study. J Assist Reprod Genet 13, 19-22.
Kotaska A (2004) Inappropriate use of randomised trials to evaluate
complex phenomena: case study of vaginal breech delivery. BMJ 329,1039-
Kutteh WH (1999) Recurrent pregnancy loss: an update. Curr Opin
Obstet Gynecol 11: 435-439.
Lee RM and Silver RM (2000) Recurrent pregnancy loss: summary and
clinical recommendations. Semin Reprod Med 2000, 18: 433-440.
Lessey BA (2000) The role of the endometrium during embryo
implantation. Hum Reprod 15 Suppl 6: 39-50.
Levran D, Farhi J, Nahum H, Royburt M, Glezerman M and Weissman A
(2002) Prospective evaluation of blastocyst stage transfer vs. zygote
intrafallopian tube transfer in patients with repeated implantation
failure. Fertil Steril 77, 971-977.
McCormack J and Greenhalgh T (2000) Seeing what you want to see in
randomised controlled trials: versions and perversions of UKPDS data. BMJ
Sackett DL, Rosenberg WM, Gray JA, Haynes RB and Richardson WS (1996)
Evidence based medicine: what it is and what it isn't. BMJ 312, 71-72.
Seif MW, Edi-Osagie ECO, McGinlay P, Blake D and Brison D (2002)
Assisted hatching for assisted conception (IVF & ICSI) (Protocol for a
Cochrane Review). In: The Cochrane Library, Issue 2. Oxford: Update
Simon C and Pellicer A (2000) Blastocyst transfer for couples with
multiple IVF failures? Fertil Steril 73, 872.
Simon SD (2001) Is the randomized clinical trial the gold standard of
research? J Androl 22, 938-943.
Spandorfer SD, Barmat LI, Navarro J, Liu HC, Veeck L and Rosenwaks Z
(2002) Importance of the biopsy date in autologous endometrial cocultures
for patients with multiple implantation failures. Fertil Steril 77, 1209-
Stevenson FK, Sahota SS, Ottensmeier CH, Zhu D, Forconi F and Hamblin
TJ (2001) The occurrence and significance of V gene mutations in B cell-
derived human malignancy.
Adv Cancer Res 83, 81-116.
Tribut O, Lessard Y, Reymann JM, Allain H and Bentue-Ferrer D (2002)
Med Sci Monit 8, 152-163.
Tucker MJ (1990) Periimplantational events post-IVF. Int J Fertil
Table 1 - New treatment is beneficial in a subgroup, but not for other patients. Table Legend: Scenario in which a new treatment is tested that is beneficial for a subgroup of patients (B-patients), but has no effect for the other patients (G-patients) (Pr = pregnant; N Pr = not pregnant; Pr% = pregnancy rate) Total N Pr Pr Pr% G-patients Treatment 900 540 360 40% Control 900 540 360 40% B-patients Treatment 100 60 40 40% Control 100 90 10 10% Total Treatment 1000 600 400 40% Control 1000 630 370 37%
Table 2 - New treatment is beneficial for most patients, but not for a subgroup. Table legend: Scenario in which a new treatment is tested that is beneficial for most patients (G-patients), but has no effect for the other patients (B-patients) (Pr = pregnant; N Pr = not pregnant; Pr% = pregnancy rate). Total N Pr Pr Pr% G-patients Treatment 900 450 450 50% Control 900 630 270 30% B-patients Treatment 100 90 10 10% Control 100 90 10 10% Total Treatment 1000 540 460 46% Control 1000 720 280 28%
Competing interests: Table 1 - New treatment is beneficial in a subgroup, but not for other patients.Table Legend: Scenario in which a new treatment is tested that is beneficial for a subgroup of patients (B-patients), but has no effect for the other patients (G-patients) (Pr = pregnant; N Pr = not pregnant; Pr% =pregnancy rate)Total N Pr Pr Pr%G-patients Treatment 900 540 360 40%Control 900 540 360 40%B-patients Treatment 100 60 40 40%Control 100 90 10 10%Total Treatment 1000 600 400 40%Control 1000 630 370 37%
To the editor: It is not a question of rejecting RCTs as a
methodology. It is only about the methodology of particular RCTs and if
they were well-constructed and if some conditions of the trial might or
might not have external validity. RCTs are "is" studies. They say that
something is or is not apparently true for the conditions under which the
trial was constructed. For other conditions/settings/groups of
practitioners that truth may not be a reality. "Why" studies try to
determine why something appears to be true or not. RCTs are not "why"
For some German and Scandinavian practitioners who did not join the
Term-Breech Trial the "conditions" of the trial did not represent their
reality, so they declined to participate as they determined in advance
that the results could not have enough external, or in their case, local
validity to induce them to participate. From the discussion so far we can
probably deduce that the Term-Breech trial had truth for the conditions of
the trial. The discussion is only about if the conditions of the Trial
represented most clinical realities or only the realities of that trial
I would like to use some material from our own RCT of episiotomy to
illustrate some of these points. Obviously we thought that we had
constructed a good trial and most people seemed happy with the results
i.e. they confirmed what they believed. But let’s look a deeper. For the
most part outcomes in the two arms of our classical RCT analyzed by
intention to treat were equivalent, except for a little of extra benefit
for multips in the restricted episiotomy arm. That was enough for most
people, as the proponents of routine episiotomy had claimed superiority of
routine episiotomy. But further study showed that for nulliparous women,
3rd/4th degree tear rates ran about 12-13% which seemed rather high as few
people had rates so high outside the trial (sound familiar?). This caused
us to look inside the trial for a "why" answer. What we found was that
some practitioners regardless of trial arm had 3rd/4th degree tear rates
in excess of 20% and others rarely if ever had such tears. Similarly some
practitioners (the same ones), almost never had a patient with an intact
perineum while others had them almost all the time.
Hence if we looked at the trial not by intention to treat but by the
behaviour of the practitioners within the trial, we found out another
truth. Those practitioners, regardless of trial arm, who truly limited
their episiotomy use, had superior results (no severe tears and lots of
intact perineums) while those who had trouble following the trial protocol
and either could not randomize very often or when randomized did
episiotomy almost all the time, "owned" the severe tears and none of the
intact perineums (sound familiar)?
We do not reject the RCT that we ran; we just found that aditional
interesting information came from a detailed analysis of what was going on
inside the trial. If the trial were reanalyzed after eliminating "non-
compliant" physicians, who after all really did not know how to attend
birth without episiotomy, the results would dramatically favour episiotomy
limitation--even by intention to treat. Without thinking hard about the
meaning of the trial, we would know less than we now know.
I think that the Term-Breech Trial perhaps can tell us additional
important information if it were further analyzed by subgroups according
to the proportion of breech births delivered vaginally at each
participating study site or site groupings--before the trial was launched.
Our sub analyses were published in various articles, perhaps the most
interesting being the one from the CMAJ on beliefs and behaviour:
1. Klein MC, Gauthier R, Robbins J, Kaczorowski J, Jorgensen S,
Franco E, Johnson B, Waghorn K, Gelfand M, Guralnick M, Luskey G, Joshi J:
Relation of Episiotomy to Perineal Trauma and Morbidity, Sexual
Dysfunction and Pelvic Floor Relaxation. American Journal of Obstetrics
and Gynecology. 1994:171 (3):591-8.
2. Klein MC, Kaczorowski J, Robbins JM, Gauthier RJ, Jorgensen SH, Joshi
AK: Physician Beliefs and Behaviour within a Randomized Controlled Trial
of Episiotomy: Consequences for Women under their Care. Can Med Assoc J.
See also supporting editorial: Schulz KF: Unbiased Research and the
Human Spirit: The Challenges of Randomized Controlled Trials [editorial].
Can Med Assoc J. 153 (6):783-786, September 15, 1995, and Graham I: I
Believe Therefore I Practise [commentary on our work]. Lancet 347:4-5,
January 6, 1996
3. Klein M: Studying Episiotomy: When Beliefs Conflict with Science. J
Fam Practice. 1995: 41(5):483-8.
4. Klein M, Janssen PA, MacWilliams L, Kaczorowski J, Johnson B:
Determinants of vaginal/perinealIntegrity and pelvic floor functioning in
childbirth. Am J Obstet & Gynecol. 1997;176:403-10.
Michael C. Klein, MD, CCFP, FAAP(Neonatal-Perinatal),FCFP, ABFP
Emeritus Professor of Family Practice and Pediatrics
University of British Columbia, Room L309B Shaughnessy Building,
Faculty Centre Community and Child Health Research,
BC Research Institute for Children's and Women's Health,
4500 Oak Street,
Vancouver, V6H 3N1
Competing interests: No competing interests
At the beginning of the Term Breech Trial, our centre deliberated
extensively over the trial protocol. Over 15 years, we have accumulated a
large volume of experience with breech birth (1500 births). Through audit
of our results, we determined that vaginal delivery is safer than planned
cesarean section and does not lead to higher perinatal mortality or
neonatal morbidity. After long discussions, we decided on ethical grounds
not to participate in the Term Breech Trial. For years, our vaginal
delivery rate for breech presentation has been over 60%.1 To have taken
part would have meant that 90 to 100% of women with a breech presentation
randomised to elective cesarean section would receive a cesarean section.
Without the trial, over 60% of these women delivered vaginally. The excess
surgical intervention without neonatal benefit was unjustifiable.
For us, the question whether a planned cesarean section or a planned
vaginal birth is safer for the newborn had already been answered. Through
close neonatal follow-up, we have observed that the excess early morbidity
associated with vaginal breech delivery stems primarily from respiratory
acidosis (pH < 7.2, Base deficit < 15), of no long term consequence
for normally grown term newborns. A German group demonstrated in 621
breech children followed to 56 months of age that the mode of delivery had
no influence on long-term neurological morbidity.2 Other groups have
reached the same conclusion, including the Term Breech Trial Collaborative
Group in their recently published 2-year follow-up.3,4,5
The complexity of birth, particularly birth from a breech
presentation, does not lend itself easily to investigation through a
protocol in which many deciding factors can only be described. Experience
and expertise can not be transferred through a protocol. For a safe
vaginal breech birth, meticulous risk assessment, case selection, and
peripartum management are prerequisites, and the structure of the birthing
unit and immediate availability of an experienced operative obstetrician
are of paramount importance. As this is also true for the safe vaginal
delivery of twins, we have similarly declined to participate in the Twin
Birth Study, also led by Professor Hannah.6 Our vaginal delivery rate for
dichorionic twins, irrespective of the presentation of Twin 1, is 75%,
without increase risk to Twin B in an audit of over 500 twin births. The
Twin Birth Study will have the same short-term endpoint and the same
problems with external validity as outlined in Dr. Kotaska’s article.7
Again, large-scale randomisation is an inappropriate method of
In contrast, our unit has eagerly embraced the large, multicenter
randomised Multiple Antinatal Corticosteroids (MACS) trial, also from
Professor Hannah’s unit.8 The methodology, including a blinded placebo
control arm, is well suited to the question of whether multiple courses of
steroids improve short and long-term neonatal outcome in the context of
threatened premature birth.
In Bavaria, 3845 term breech deliveries occurred in 2003. Despite the
results of the Term Breech Trial, the proportion of breeches delivered by
elective cesarean section has dropped from 71.1% in 2000 to 63.7%% in
2003.9 In Nürnberg, we have not altered our management and continue to
recommend planned vaginal birth in over 90% of breech presentations.
1.Feige, A; Krause, M: Beckenendlage (Breech Presentation), Urban
& Schwarzenberg, 1998
2.Wolke, D; Söhne, B; Schulz, J; Ohrt, B; Riegel, K: Die kindliche
Entwicklung nach vaginaler und abdominaler Entbindung bei Beckenendlage.
In: Beckenendlage. Feige, A, Krause, M (eds.), Urban & Schwarzenberg
3.Danielian, PJ; Wang, J; Hall, MH: Long term outcome by method of
delivery of fetuses in breech presentation at term: population based
follow up. BMJ 1996;312:1451-3
4.Munstedt, K; von Georgi, R; Reucher, S; Zygmunt, M; Lang, U: Term
breech and long-term morbidity – caesarean section versus vaginal breech
delivery. Eur J Obstet Gynecol Reprod Biol 2001;96(2):163-7
5.Whyte, H at al. for the 2-year infant follow-up Term Breech Trial
Collaborative Group: Outcomes of children at 2 years after planned
cesarean birth versus planned vaginal birth for breech presentation at
term: The International Randomized Term Breech Trial. Am Obstet Gynecol
7.Kotaska, A: Inappropriate use of randomisation trials to evaluate
complex phenomena: case study of vaginal breech delivery. BMJ
9.Bayerische Arbeitsgemeinschaft für Qualitätssicherung in der
stationären Betreuung. Qualitätsbericht Geburtshilfe, Jahresauswertungen
Competing interests: No competing interests
Not every decision requires a randomized trial. For example, the use
of parachutes! (1) But this powerful method of investigation has often
usefully informed our practices and added evidence to help with making the
choices that can be done in consultation by doctors and patients. The
randomization controls for the biases of which we are aware and, even more
importantly, the ones of which we are not aware.
Now Andrew Kotaska has argued in a BMJ article (BMJ 2004; 329:1039-
42) that randomized trials cannot appropriately be used to evaluate
complex phenomena, using the recent Term Breech Trial as an example. He
further alleges that the conduct of the trial may have led to an
inappropriately poor standard of care.
I think he is wrong on both counts. Here is why:
I fully acknowledge the complexities of both judgment and skill that
go into the decision of whether or not to attempt a vaginal delivery when
the fetus is in breech presentation, of more judgment during the conduct
of labour, if that is chosen, and skill for the performance of the
manoeuvers to assist with the delivery. Despite the claim that this
constitutes a limitation on the proper use of a randomized trial, it is
precisely because of this degree of complexity, particularly with
judgment, that may allow the inapparent creeping in of bias, that a
randomized trial is required for evaluation.
Cohort and other trials of vaginal breech delivery have demonstrated,
in some instances, a remarkably good outcome. This may simply illustrate
very good judgment by a few unusually good physicians in selecting which
patients should attempt a vaginal birth breech. It may also reflect
judgment as to which groups of patients to report in the literature.
Randomized trials may indeed be applied to complex conditions and
reveal differences that otherwise might not be apparent. An example is
the application of fetal endoscopic tracheal occlusion for management of
congenital diaphragmatic hernia. This intervention was biologically
highly plausible, and initial, uncontrolled observations, as is often the
case when new procedures are performed by enthusiasts, yielded optimistic
results. The eventual trial (2) compared the new intervention to standard
care. Both were highly complex packages of care. Despite the
expectations of the investigators at the beginning of the trial, it was
stopped after 24 patients had been enrolled because there was no
improvement in survival or morbidity. There was a substantial initial
intervention and then a cascade of various events associated with the
intervention ( have we heard that before?) The randomized trial provided
the basis for decision-making as to whether to continue this intervention
or, wisely, not.
Evaluation of interventions with respect to their effectiveness has
been increasingly called for in surgery. (3) In calling for a most
effective evaluation as to whether complex procedures are effective (4),
it is noted that “although clinical observations can provide important
insights, thet are limited by lack of objectivity.”
Examples of contradictory observational and randomized trial results
are not restricted to medical interventions and are found for procedural
interventions. Because most interventions have moderate rather than large
treatment effects, they are the ones most susceptible to misleading
conclusions from observational studies. The performance of an episiotomy
is a less complex matter of both judgment and skill than breech delivery
but this intervantion was usefully studied in randomized trials. It is the
results of those randomized trials that contributed to a desirable (
because of what we know from the randomized trial results) reduction in
the previously "normal routine" provision of episiotomy.
Andrew Kotaska uses the concept of “bias of licence” to suggest that
perhaps there was some suspension of the normal devotion to good care and
safety of patients, which he alleges practitioners may have done by
increasing too much the number of breech deliveries they did. It is
implied that the quality of care may have been inferior in the breech
trial. I must acknowledge my bias at this point. Ours was one of the
participating centres in the Term Breech Trial, and I was one of the
practitioners who delivered women who had been randomized. I was hoping
to achieve a good outcome for the patients randomized to vaginal delivery
of a breech (which is not actually different from what I hope for for all
of the patients for whom I have the privilege to provide care). I can
speculate that there may have been more than the usual pressure to resort
to a caesarean section if it seemed the outcome might not be good by
proceeding with a vaginal delivery to avoid having bad outcomes with fetal
entrapment in the vaginal delivery group.
The comparison of the rates of vaginal deliveries of women with
fetuses in breech presentation may be spurious. The calculation of 13
percent of all breeches being delivered vaginally in centres participating
in the Term Breech Trial would include in the denominator women with
breeches who were not suitable for vaginal delivery and others who
declined having an attempted vaginal delivery. By important contrast, the
minimum 40 percent actual vaginal births sought in the limb of the Term
Breech Trial for women randomized to attempt a vaginal delivery would have
included only women who met the stringent inclusion criteria defined by a
consensus of experts and who were willing to accept randomization to the
possibility of vaginal delivery. The subsequent conduct of the labour for
each individual woman randomized to attempt a vaginal delivery would then
have been done with the judgment, skill, and commitment to good care by
Achievement of at least a 40 percent actual vaginal birth rate in
this selected group is consistent with that of cohort studies from other
centres with similar maternal consent and expert selection and conduct of
the labour and delivery as noted by Dr. Kotaska. Achievement of such
numbers should not only be not surprising but reasonably expected.
In any case, the evidence from a variety of trials is that the
outcome of care provided within a trial is generally better than the
outcome of comparable care for comparable conditions provided outside of
the trial. (5,6) The first of these references notes that “clinical
trials have a positive rather than negative effect on the outcome of
patients.” In larger trials where effective treatment already exists and
is included in the trial protocol (and that surely applied to the Term
Breech Trial) whichever limb one would regard as “effective” has better
results for trial participants.
It is, of course, a matter of judgment whether to apply the results
of any randomized trial to a care of one’s own patients. Included in that
judgment is the determination of the individual practitioner as to whether
the trial itself was well done and whether the patients in the populations
studied are sufficiently like the population of the individuals within the
population cared for by the practitioner to be applicable to them.
One can always argue that each individual is unique, and yet in the
practice of medicine we must also be appropriately guided by what works
for most of the people most of the time since that is most likely to apply
to the work that we are doing. It is advanced as a criticism of the Term
Breech Trial that this involved multiple practitioners and multiple sites,
and yet it is just that fact that may make its findings more
generalizeable. The speculation by Dr. Kotaska in his paper that
practitioners were somehow induced “to exceed their comfort level with
vaginal breech delivery” is only speculation and is inconsistent with the
results from the evaluation of the outcomes of care in other trials.
Of the two options within the term breech trial, I argue that the
judgment and skill to perform a vaginal breech delivery is probably more
complex and demanding than doing a caesarean section. Thus, the
improvement in performance, which is a characteristic of the outcome of
care within the context of a clinical trial, is more likely to have been
beneficial for the vaginal breech deliveries in the trial than for the
caesarean section limb. In other words, the short term disadvantage of
intended vaginal delivery of a breech fetus is likely to be wider in the
real world than in the trial results.
The two-year follow-up results of the term breech trial have, of
course, just recently been published and have demonstrated no difference
in the long-term outcomes for a subgroup in the trial which is different
from the composite short-term results. This is consistent with much data
about the inherent toughness of newborns who tend to do quite well in the
long-run, even with unfavourable immediate assessments.
I, too, was very disappointed in the outcome of the term breech
trial. I like delivering breeches vaginally, and I am still willing to do
so for women who appear likely to succeed and who, after consideration of
the available information and their own particular situation, want to try
for a vaginal delivery. I had hoped that the term breech trial would have
provided an outcome more consistent with my pre-trial hopes and contribute
to reversing the trend to increasing caesarean section delivery of
breeches. Disappointment at the message, however, should not lead to
disparaging comments about the messengers or denigration of the
methodology leading to the message. We owe our patients and our
professional integrity a greater devotion to the acquisition and use of
the best available relevent information., so that we can use that
information when we are decision making with our patients.
1. Gordon C.S. Smith, Jill D. Pell. Parachute Use to Prevent Death in
Major Trauma Related to Gravitational Challenge: Systematic Review of
Randomized Controlled Trials BMJ 2003; 327: 1450.
2. Michael R. Harrison, Roberta L. Keller, Samuel B. Hawgood et al N
Engl J Med 2003; 349: 1916-24.
3. Moritz N. Wente, Christoph M. Seiler, Waldemar Uhi, Markus Buchler
Dig Surg 2003;20: 263-269.
4. P.J. Devereaux, Michael D. McKee, Salim Yusuf. Methodologic
Issues in Randomized Controlled Trials of Surgical Interventions, Clin
Orthopedics and Related Research 2003; 413: 25-32.
5. David A. Braunholtz, Sarah JL Edwards, Richard J Lilford Are
randomized clinical trial good for us (in the short term)? Evidence for a
"trial effect." J Clin Epidemiology 2001; 54: 217-224.
6. Al Hallstrom, Lawrence Friedman, Pablo Denes, Carlos Rizo-Patron,
Mary Morris and the CAST and AVID Investigators Do arrythmia patients
improve survival by participating in randomized clinical trials?
Observations from the cardiac arrhythmia suppression trial (CAST) and the
Antiarrhythmics Versus Implantable Defibrillators Trial (AVID) Controlled
Clinical Trials 2003: 24: 341-352.
Competing interests: No competing interests
Isabelle Boutron, MD*, Bruno Giraudeau PhD**, Philippe Ravaud, MD,
*Département d’Epidémiologie, Biostatistique et Recherche Clinique,
INSERM EMI 0357, Groupe Hospitalier Bichat-Claude Bernard (AP-HP), Faculté
de Médecine Xavier Bichat, Université Paris VII, 75018 Paris, France
**INSERM CIC 202, Tours, France
The article by Kotaska(1) outlines the important issue related to
care providers’ skill and settings’ experience when assessing
nonpharmacological treatments such as vaginal breech delivery in
randomised controlled trials (RCT). We agree that the evaluation of
nonpharmacological treatments raises specific methodological issues, among
them care providers’ skill(2). Actually, in RCTs of nonpharmacological
treatment, care providers are also part of the intervention to be tested,
and bias could occur with (i) highly skilled or experienced care providers
in one arm and low-skilled or less-experienced care providers in the other
or (ii) care providers with more experience in performing one of the
interventions tested than another. However, appropriate methodological
organisation and planning of RCTs in this field could circumvent this
bias. Thus, care providers in a trial of surgery could be trained and
selected only if they achieved a predetermined standard(3) or selected
according to their experience of the procedure. For example, in a trial
assessing carotid endarterectomy, each surgeon had their last 50
operations assessed and if more than 2 of the operations resulted in
complications the surgeons could not join the trial(4). Such a
prerequisite then allows the surgical procedure to be assessed in the
context of the skills required to achieve it. As well, patients could be
randomised not to operations but to care providers, who would perform
their treatment of preference, thus ensuring similar skill levels in the
two arms of the trial(5).
Thus, although this article was an interesting example of potential bias
linked to care providers’ experience in an RCT assessing
nonpharmacological treatment, the author generalizes sweepingly when
concluding that “complex procedures are poorly amenable to the methods of
large multicentre randomised trials”. To condemn multicentre RCTs
assessing complex interventions because of one imperfect RCT appears as
inappropriate as defining a new standard of care for vaginal breech
delivery on the basis of a unique and potentially biased trial.
1.Kotaska A. Inappropriate use of randomised trials to evaluate
complex phenomena: case study of vaginal breech delivery. BMJ. Oct 30
2.Boutron I, Tubach F, Giraudeau B, Ravaud P. Methodological
differences in clinical trials evaluating nonpharmacological and
pharmacological treatments of hip and knee osteoarthritis. JAMA. Aug 27
3.Feldon SE, Scherer RW, Hooper FJ, et al. Surgical quality assurance
in the Ischemic Optic Neuropathy Decompression Trial (IONDT),. Controlled
Clinical Trials. 2003;24:245-354.
4.Barnett HJ, Taylor DW, Eliasziw M, et al. Benefit of carotid
endarterectomy in patients with symptomatic moderate or severe stenosis.
North American Symptomatic Carotid Endarterectomy Trial Collaborators. N
Engl J Med. Nov 12 1998;339:1415-1425.
5.McCulloch P, Taylor I, Sasako M, Lovett B, Griffin D. Randomised
trials in surgery: problems and possible solutions. BMJ. 2002;324:1448-
Competing interests: No competing interests
In his penetrating analysis of the Breech Trial reported by Hannah M.
E. et al. Lancet 2000;329: 1375-83 Dr. Andrew Kotaska, with devastating
lucididity, examines the defects in the report and the potentially serious
implications of its uncritical acceptance. It seems remarkable that an
article which may subject thousands of women to a major surgical procedure
should have elicited no editorial response. For a prestigious journal to
publish so significant a report without careful assessment by experienced
obstetricians, or at least so it would appear for there is no other
obvious explanation, and to have to have the shortcomings brought to the
attention of the profession through the report of a Senior Registrar Dr.
Andrew Kotaska BMJ.2004;329: 1039-1042 (30 October 2004) is unfortunate,
to say the least.
Competing interests: No competing interests
The Term Breech Trial Collaborative Group are to be commended for
their comprehensive two-year follow-up of their trial.1 The widely touted
short-term advantage of elective cesarean section over planned vaginal
birth has disappeared. Eighteen infants with “serious (early) morbidity”
as defined by experts were followed, and seventeen were neurologically
normal at two-years of age. Even with the average level of care and the
bias of license present in the trial, 97% of women in both groups had a
normal child, rendering further debate about the trial’s external validity
Professor Hannah brings attention to the varying rates of vaginal
delivery in the literature. She and I both cite Irion and Schiff, who
participated in the term breech trial and who, in their own retrospective
series, delivered 39% of all breeches vaginally, with less mortality and
short-term morbidity than the term breech trial.2,3 She misses the point.
Such experienced centres exist, but were under-represented in the term
breech trial (Irion and Schiff out of 121 centres). Why did none of the
published centres from Austria, France, Ireland, Germany, Sweden, or
Norway participate? In Norway, 40% of breech deliveries are vaginal vs.
12% in North America. Some of these European centres with demonstrated
safety and expertise in vaginal breech delivery, including the most
experienced unit in Germany, deemed the trial protocol unsafe and declined
to participate in the trial. This constitutes a selection bias that
resulted in a lower than average level of care within the trial.
It is difficult to compare overall vaginal delivery rates because
individual units allow vastly different proportions of women with a
breech to labour(32% to 94%).4,5 Regardless, our maternity unit, the
largest in Canada, delivers 200+ breech babies from 7000 births annually.
Before the term breech trial, 12% of these delivered vaginally: one per
consultant and per registrar per year and one per labour nurse every 5
years. This rate is average for North America, and reassurances about “the
presence of a skilled practitioner” aside, it does not represent a body of
expertise with vaginal breech delivery. Varying levels of expertise would
be expected to result in varying rates of successful, safe vaginal
delivery. Demanding all units achieve a 40+% vaginal delivery rate in a
trial setting certainly invited some of them to push their limits. Despite
Professor Hannah’s doubts about the existence of a bias of license,
comfort level at the edge of one’s capabilities is a delicate and etherial
Professor Hannah’s suggestion that the safety and success of
experienced units can be defined in a reductionist fashion with selection
criteria and restrictive protocols also misses the point. These units are
by no means uniform, having developed a variety of strategies and safety
measures and some unifying philosophies over years. Success rates vary
widely from 14% to 66% of all breech presentations.5,6 Like many complex
human skills, expertise is acquired through mentorship and attention to
detail and cannot be adequately defined or exported via written protocols.
The recent Norwegian audit suggests that even for experienced units,
pushing the envelope will at some point compromise safety.7 Each
practitioner (and unit) has his/her own level of comfort and capability.
Pushing this level demands caution, whether with vaginal hysterectomy or
breech delivery; safety will be compromised if one pushes too hard.
Professor Hannah’s call to centres demonstrating expertise and safety
with vaginal breech delivery to mount another randomised trial suggests an
uncritical enthusiasm for large-scale randomisation. Maternity units that
have proven safety with adequate numbers through meticulous self-audit
have no need for a randomised trial. They understand the complex nature of
the phenomenon, the dependence of success and safety on careful
development and maintenance of expertise, and the inability to describe,
teach or ensure this expertise with written protocols, even those from
Professor Hannah’s research unit. Consequently, some have also declined to
participate in her randomised study of elective cesarean section in twin
gestations: another selection bias.
The rapid transformation of the early term breech trial results into
clinical practice guidelines has effectively eliminated the option of
vaginal breech delivery for most women in North America and the U.K.8,9
With publication of the 2-year follow-up showing no difference in long-
term outcome, many women will again desire a trial of labour. Our task is
to learn from the remaining centres demonstrating expertise in vaginal
breech delivery and carefully re-establish the skill in motivated centres.
New guidelines are urgently needed to release the choke-hold of the early
term breech trial results on clinical practice and re-establish choice for
women. Despite the unquestionable utility and power of randomised trials,
the safety of some complex procedures may be more effectively demonstrated
through careful self-audit than through large-scale randomisation. Perhaps
new guidelines should reflect this.
1.Whyte H, Hannah ME, Saigal S, Hannah WJ, Hewson S, Amankwah K, et
al. for the 2 year infant follow-up Term Breech Trial Collaborative Group.
Outcomes of children at 2 years after planned cesarean birth vs. planned
vaginal birth for breech presentation at term: the international
randomized Term Breech Trial. Am J Obstet Gynecol 2004;191:864-71
2.Irion O, Almagbaly PH, Morabia A. Planned vaginal delivery versus
elective cesarean section: a study of 705 singleton term breech
presentations. Br J Obstet Gynecol 1998;105:710-7
3.Schiff E, Friedman SA, Mashiach S, Hart O, Barkai G, Sibai BM.
Maternal and neonatal outcome of 846 term singleton breech deliveries:
seven year experience at a single centre. Am J Obstet Gynecol 1996;175:18-
4.Sanchez-Ramos L, Wells TL, Adair CD, Arcelin G, Kaunitz AM, Wells
DS. Route of breech delivery and maternal and neonatal outcomes. Int J
Gynaecol Obstet 2001;72:7-14
5.Krause PM. (Nürnberg breech study: is cesarean section the better
mode of delivery for the child?) Hebamme 2001;14(3):137-147
6.Hauth JC, Cunningham FG. Vaginal breech delivery is still
justified. Obstet Gynecol 2002;99:1115-6
7.Haheim LL, Albrechtsen S, Berge LN, Bordahl PE, Egeland T, Henri
Oian P. Breech birth at term: vaginal delivery or elective cesarean
section. A systematic review of the literature by a Norwegian review team.
Acta Obstet Gynecol Scand. 2004 Feb;83(2):121-3
8.ACOG Committee Opinion No. 265. Mode of term singleton breech
delivery. December 2001. American College of Obstetricians and
Gynecologists. Int J Gynaecol Obstet 2002;77(1):65-6
9.RCOG Guidelines: Clinical Green Top Guidelines: The Management of
Competing interests: No competing interests
One of the articles in your recent themed issue of Evidence Based
Medicine featured a photograph (page 1039) illustrating a vaginal breech
delivery. In the photograph the midwife is preparing to suction meconium
from the baby’s oropharynx using a device that generates suction from her
mouth. Ironically there is ample evidence that oropharyngeal suction does
not prevent meconium aspiration syndrome and there is also an infection
risk to the midwife from accidental ingestion of the said meconium.
Vain NE. Szyld EG. Prudent LM. Wiswell TE. Aguilar AM. Vivas NI.
Oropharyngeal and nasopharyngeal suctioning of meconium-stained neonates
before delivery of their shoulders: multicentre, randomised controlled
trial. Lancet. 364(9434):597-602, 2004
Ballard JL. Musial MJ. Myers MG. Hazards of delivery room
resuscitation using oral methods of endotracheal suctioning. Pediatric
Infectious Disease. 5(2):198-200, 1986
Competing interests: No competing interests
The dramatic results of the Term Breech Trial, which have influenced
clinical practice worldwide, are continuing to stimulate discussion and
debate. Dr Kotaska’s article questions the generalisability or external
validity of the trial results.
Dr Kotaska suggests that a vaginal delivery rate of 57% in the
planned vaginal birth group of the Term Breech Trial (68% in countries
with a high national perinatal mortality rate; 45% in countries with a low
perinatal mortality rate), is higher than would occur in experienced
centres. We disagree. Published rates of vaginal breech delivery among
those women having a trial of labour (thus excluding the many women having
an elective caesarean) are actually very similar or higher than what
occurred in the planned vaginal birth arm of Term Breech Trial.1-3 Dr
Kotaska also suggests that practitioners in the Term Breech Trial
increased their vaginal delivery rates beyond their comfort level. Does Dr
Kotaska mean to imply that a practitioner would undertake a vaginal breech
delivery that he or she did not feel comfortable doing, simply because the
woman was in the Term Breech Trial? We believe that such a practice would
be unethical, unprofessional, and unlikely given the current medico-legal
climate in many of our countries.
We agree that surgical and other complex procedures are more
difficult to evaluate than medical interventions, and that operator
expertise is of crucial importance. Indeed, in the Term Breech Trial, the
presence of a skilled and experienced practitioner at vaginal breech
delivery was significantly associated with better outcome for the baby.4
However, although variation in operator expertise and technique is
inherent in surgical procedures, randomised controlled trials continue to
provide the best evidence as to whether these procedures result in more
good than harm. We sympathize with the many practitioners who do not
believe that the results of the Term Breech Trial apply to them. No one
was more disappointed with the findings of the trial than the Term Breech
Trial collaborating clinicians who were hoping to prove the safety of
vaginal breech delivery, and who, by participating in the trial,
collectively put their vaginal breech delivery skills to the test.
Dr Kotaska criticizes the selection criteria and the intrapartum
management protocol of the Term Breech Trial as being too broad and
suggests that the results of the Term Breech Trial do not apply in centres
that have more restrictive criteria and protocols. The Term Breech Trial
protocol was developed by a group of obstetricians who were recognised in
their communities as experts at vaginal breech delivery, and was vetted by
experienced obstetricians worldwide prior to beginning the trial and while
it was in progress.5 However, if others support the view that the question
of how best to deliver some women with a singleton fetus in breech
presentation at term, using a more restrictive protocol, is still
unanswered, we would encourage them to enroll their patients in a
randomised controlled trial, so that we can learn whether a policy of
caesarean is (or is not) better than a policy of vaginal breech delivery
for these more highly selected women using these more restrictive
Finally, for those women preferring a vaginal breech birth, they
should be reassured that although planned caesarean section reduced the
risk of perinatal or neonatal mortality or serious neonatal morbidity,
compared to planned vaginal birth, in the Term Breech Trial, 95% of babies
in the planned vaginal birth arm did well. Also, although our statistical
power was limited, we did not find planned caesarean to be associated with
better outcomes for the children at 2 years of age.6
1. Sanchez-Ramos L, Wells TL, Adair CD, Arcelin G, Kaunitz AM, Wells DS.
Route of breech delivery and maternal and neonatal outcomes. Int J
Gynaecol Obstet 2001;73:7-14.
2. Schiff E, Friedman SA, Mashiach S, Hart O, Barkai G, Sibai BM. Maternal
and neonatal outcome of 846 term singleton breech deliveries: seven-year
experience at a single center. Am J Obstet Gynecol 1996;175:18-23.
3. Irion O, Almagbaly PH, Morabia A. Planned vaginal delivery versus
elective cesarean section: a study of 705 singleton term breech
presentations. Br J Obstet Gynaecol 1998;105:710-7.
4. Su M, McLeod L, Ross S, Willan A, Hannah WJ, Hutton E, Hewson S, Hannah
M for the Term Breech Trial Collaborative Group. Factors associated with
adverse perinatal outcome in the Term Breech Trial. Am J Obstet Gynecol
5. Hannah WJ, Allardice J, Amankwah K, Baskett T, Cheng M, Fallis B,
Farquharson D, Gauthier R,
Hannah M, Hewson S, Lalonde A, Lange I, Milne K, Mitchell B, Penkin P,
Ritchie K, Hackett G, Walkinshaw S, Turner M. The Canadian consensus on
breech management at term. J SOGC 1994;
6. Whyte H, Hannah ME, Saigal S, Hannah WJ, Hewson S, Amankwah K, Cheng M,
Gafni A, Guselle P, Helewa M, Hodnett E, Hutton E, Kung R, McKay D, Ross
S, Willan A for the 2 year infant follow-up Term Breech Trial
Collaborative Group. Outcomes of children at 2 years after planned
cesarean birth vs planned vaginal birth for breech presentation at term:
the international randomized Term Breech Trial. Am J Obstet Gynecol
Competing interests: No competing interests