Analysing all the data showed no differences in the rates of any form of infection in the women or their babies for at least one month after the birth.
There was a slight trend towards labours being shorter in women given enemas. Note: Content may be edited for style and length.
Science News. ScienceDaily, 18 October Retrieved November 9, from www. Choosing to induce A puerperal outcome was positive when, during the first month after delivery, a health care provider diagnosed the women with any of the following: dehiscence of the episiorraphy suture, purulent effusion from the episiorraphy, urinary tract infection, pelvic inflammatory disease, or vulvovaginitis.
The primary outcome of the study was an aggregated maternal and neonatal infection rate: either the mother or the newborn had an infectious outcome combined infection rate.
A team member visited participating women and newborns in hospital on a daily basis. Throughout the trial, trained research assistants using standardised questionnaires, registered data from telephone calls, hospitalisations, follow-up visits, and any communications with the participants, their families, or their health care providers.
Masking the use of enemas was unfeasible. However, we made efforts to conceal the intervention by not separating documents with information on the allocation from those outcome data collection, by training the team's supporting clinical team professional nurse, family medicine residents, family medicine staff, and consulting dermatologist to avoid enquiring in ways that would unmask the allocation.
Health care providers in other settings, such as physicians at emergency wards, paediatricians and medics at outpatient clinics were unaware of the allocation and frequently of the specific objectives of the study.
Except for the intervention, participants received the same health care, and data retrievers would remain unaware of individual allocations. Interventions remained coded for the analysis and the code was broken once the analysis was completed. Input between data at recruitment and allocation was done weeks before the collection of data on outcomes at follow up. We were unable to find reliable data on the incidence of baseline infection rates for puerperal women or newborns so we did a pilot study to have base data that would allow a good estimate of frequencies for sample size calculations.
The pilot study, which included the first 44 participants of the control group, estimated the combined infection rate of puerperal women and newborns at 46 percent [ 7 ]. The database created in Epi-Info v 6. A Shapiro-Wilk test was used to determine if the distribution of continuous variables was normal.
Non-normal distributions were transformed using a log transformation, and if the distribution was persistently non-normal, a Mann-Whitney test was used to compare groups. Bivariate analyses were done using the chi-square test or Fisher's exact test. Power calculations were done using specialized software developed at the Clinical Epidemiology Unit at the Javeriana University[ 9 ]. During the twelve months recruitment period Feb —Feb women were admitted for delivery to the obstetric service.
Of the women interviewed for recruitment, 16 were non-eligible and 1 declined to participate. We randomised women see Figure 1 , among which we had 12 protocol violations; 4 in the enema group and 8 in the control group. Nevertheless, these women were offered the care and benefits that all other participants had.
Protocol violations included admission with ruptured amniotic membranes 5 women in the control group , infection at admission 1 in the control group, 2 in the enema group. Five women didn't fulfil inclusion criteria but were randomised 2 in the control group and 3 in the enema group.
The analysis for the remaining women was done by group of allocation. Women who delivered by caesarean section were considered in the analysis. Data were not available to include in an 'intention to treat' analysis the 12 women excluded because of violations to the selection criteria protocol violations. Baseline characteristics were similar in both groups, suggesting that randomisation provided well-balanced and comparable groups Table 1 [see additional file 2 ].
Labour duration times and other maternal outcomes were obtained from women's records after delivery and are presented in Table 2 [see Additional file 2 ]. Neonatal baseline data obtained shortly after delivery from newborns' records are summarised in Table 3 [see Additional file 2 ]. We found no statistically significant differences between groups for labour duration, delivery types, episiotomy rates, or prescription of antibiotics.
No significant differences were found in the distribution between groups for newborns' "Ballard" score, birth weight, diagnosis of neonatal apnoea, or the administration of ocular and umbilical prophylaxis.
Five newborns allocated to the control group and none in the treatment group developed respiratory tract infections, but this difference had no statistical significance.
Two out of the five newborns who developed lower respiratory tract infections were delivered by caesarean section. The three newborns with omphalitis belonged to the intervention group, but again this difference was not statistically significant. Similarly, no significant differences were found for ophthalmic infection rates, skin infections, intestinal infections or the need for systemic antibiotics Table 4 [see Additional file 2 ].
No statistically significant differences were found for any of the assessed outcomes in puerperal women. The frequency and severity of perineal tear was similar in the intervention and control group.
No significant differences were found in the rates of suture dehiscence among the women who had epysiorraphy Table 5 [see Additional file 2 ]. Summarised outcomes are provided in Table 6 [see Additional file 2 ]. Overall, one in five newborns had an infectious outcome, and rates were not statistically significant between groups. The aggregated outcome of "neonatal or puerperal infection" during the day follow-up was higher in the control group than in the intervention group.
We planned to assess the effect of enemas' on labour duration using multiple linear regression to adjust for parity. However the normality test of the variable was rejected and a Boxcox transformation with a range between -2 and 2 did not provide an appropriate model.
Described in Figure 1 [see Additional file 1 ]. Puerperal and neonatal infections, although seldom life threatening, were very frequent in this study. Ophthalmic infections were the most frequent infections amongst newborns. Breast engorgement and nipple cracking were the most frequent maternal complaints during puerperium. Episiorraphy dehiscence was the most frequent infectious outcome in women. We were impressed by how frequent these outcomes were, and it is likely that these problems are being missed in studies with a shorter follow up, such as those that only follow women during hospitalization.
It also suggests that the follow up strategy probably had a good sensitivity. High volume enemas used during the first stage of labour did not have a significant effect in the incidence of puerperal or neonatal infections, or labour duration. This RCT found no significant differences in puerperal or neonatal infection rates with enemas. No statistically significant effects were found when analysing women or newborns separately or when their outcomes were aggregated to analyse them as mother-newborn dyads.
However, the study may have been underpowered to detect differences for individual outcomes. A higher rate of operative vaginal deliveries was found in the enema group, although it did not reach statistical significance. It is worth mentioning this, because operative vaginal deliveries may have an effect in puerperal infection rates.
The use of an aggregated outcome helped to reduce sample size but it would have been ideal to have a sample size large enough to establish effects in newborns and puerperal women separately.
Despite being practical, aggregating results has important limitations: if the maternal and neonatal outcomes have significantly different magnitudes or point out in different directions, aggregation will cancelled out or underestimate the differences. We didn't have resources to collect information to assess if the population of women admitted to the trial represented all eligible women.
However, participation in the trial was apparently determined by the commitment of recruiters, not the participants' risk. The RCT did not evaluate women's preferences or known adverse effects of enemas, such as pain, discomfort, embarrassment, or diarrhoea. Since just one-fifth of the participants were personally examined by trained research assistants at the one-month assessment, measurements of these outcomes may have been imprecise and could potentially disguise existing differences, accounting for the lack of differences risk of Type II error.
No, not baby poop, but instead concerns about whether or not you might have a bowel movement while in labor. By now, most women have found that doctors are completely unfazed by it — considering that they bear witness to many fluids during birth — and so they shrug it off.
But there are still questions about the cleanup process if it does happen and even, do they give you an enema before labor? Turns out, this is an old prep method. I think it was done previously so that women did not have a bowel movement while pushing the baby out.
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