Antenatal dietary education and supplementation to increase energy and protein intake

Primary outcomes

• Perinatal mortality (defined by trialists)

• Stillbirth (death after 20 weeks' gestation and before birth)

• Neonatal death (death of a live infant within the first 28 days of life)

Secondary outcomes

(1) Random sequence generation (checking for possible selection bias)

We described for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.

We assessed the method as:

• low risk of bias (any truly random process, e.g. random number table; computer random number generator);

• high risk of bias (any non‐random process, e.g. odd or even date of birth; hospital or clinic record number);

• unclear risk of bias.

(2) Allocation concealment (checking for possible selection bias)

For each included study, we described the method used to conceal the allocation sequence in sufficient detail and determined whether the intervention allocation could have been foreseen in advance of or during recruitment, or changed after assignment.

We assessed the methods as indicated below:

• low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);

• high risk of bias (e.g. open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth);

• unclear risk of bias. 

(3.1) Blinding of participants and personnel (checking for possible performance bias)

We described for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We considered that studies were at low risk of bias if they were blinded, or if we judged that the lack of blinding would be unlikely to affect results. We assessed blinding separately for different outcomes or classes of outcomes.

We assessed the methods as:

• low, high or unclear risk of bias for participants;

• low, high or unclear risk of bias for personnel.

(3.2) Blinding of outcome assessment (checking for possible detection bias)

We described for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We assessed blinding separately for different outcomes or classes of outcomes.

We assessed methods used to blind outcome assessment as:

• low, high or unclear risk of bias.

(4) Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts, protocol deviations)

For each included study, and each outcome or class of outcomes, we described the completeness of the data including attrition and exclusions from the analysis. We stated whether attrition and exclusions were reported, the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information was reported or supplied by the trial authors, we re‐included missing data in the analyses that we undertook.

We assessed methods as indicated below:

• low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);

• high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; 'as treated' analysis done with substantial departure of intervention received from that assigned at randomisation);

• unclear risk of bias.

(5) Selective reporting bias

For each included study, we described how we investigated the possibility of selective outcome reporting bias and what we found.

We assessed the methods as indicated below:

• low risk of bias (where it was clear that all of the study's pre‐specified outcomes and all expected outcomes of interest to the review had been reported);

• high risk of bias (where not all of the study's pre‐specified outcomes have been reported; one or more reported primary outcomes were not pre‐specified; outcomes of interest were reported incompletely and could not be used; study failed to include results of a key outcome that would have been expected to have been reported);

• unclear risk of bias.

(6) Other bias (checking for bias caused by problems not covered by section (1) to (5) above)

For each included study, we described any important concerns we had about other possible sources of bias.

We assessed whether each study was free of other problems that could put it at risk of bias as indicated below:

• low risk of other bias;

• high risk of other bias;

• unclear risk of other bias.

(7) Overall risk of bias

We made explicit judgements about whether studies were at high risk of bias, according to the criteria given in the Handbook (Higgins 2011). With reference to (1) to (6) above, we planned to assess the likely magnitude and direction of the bias and whether we considered it was likely to impact on the findings. In future updates, we will explore the impact of the level of bias through undertaking sensitivity analyses ‐ seeSensitivity analysis.

Assessing the quality of the evidence

For this update the quality of the evidence was assessed using the GRADE approach (Guyatt 2008; Schunemann 2009) in order to assess the quality of the body of evidence relating to the following outcomes (maximum of seven) for the four main interventions such as dietary education, balanced protein and energy supplementation, high‐protein supplementation and isocaloric balanced protein supplementation:

1. perinatal mortality (defined by trialists);

2. stillbirth (death after 20 weeks' gestation and before birth);

3. neonatal death (death of a live infant within the first 28 days of life);

4. small‐for‐gestational age;

5. preterm birth;

6. birthweight (g);

7. gestational weight gain (kg) (including weekly gestational weight gain (g)).

GRADEprofiler (GRADEpro 2014) was used to import data from Review Manager 5.3 (RevMan 2014) in order to create ’Summary of findings’ tables. A summary of the intervention effect and a measure of quality for each of the above outcomes was produced using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of the body of evidence for each outcome. The evidence can be downgraded from 'high quality' by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias.

Dichotomous data

For dichotomous data, we presented the results as the summary risk ratio with the 95% confidence intervals. 

Continuous data

For continuous data, we used the mean difference if the outcomes were measured in the same way between trials. If necessary, we planned to use the standardised mean difference to combine trials that measured the same outcome, but used different methods.  

Cluster‐randomised trials

We included cluster‐randomised trials in the analyses along with individually‐randomised trials. We adjusted their sample sizes using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) using an estimate of the intra‐cluster correlation co‐efficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population. Where we used ICCs from other sources, we reported this and conducted sensitivity analyses to investigate the effect of variation in the ICC. We determined that if we identified both cluster‐randomised trials and individually‐randomised trials, we planned to synthesise the relevant information. We would have considered it reasonable to combine the results from both if there was little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomisation unit was considered to be unlikely. Two of the trials (Ceesay 1997; Kafatos 1989) gave no published or unpublished data on the outcome‐specific ICC. Therefore, we assumed a value of 0.01 and adjusted the corresponding sample sizes according to the design effect, i.e. by dividing the crude (individual) sample sizes by 1+ (m ‐1)r, where m is the average cluster size and r is the ICC (assumed to be 0.01). We conducted sensitivity analyses to investigate the effect of variation in the ICC (Figure 1; Figure 2).

Cross‐over trials

Cross‐over trials were not considered in this review.

Participants

Seven trials were conducted in an economically disadvantaged area including under‐nourished populations (Briley 2002; Ceesay 1997; Girija 1984; Huybregts 2009; Kardjati 1988; Mora 1978; Rush 1980); the other 10 trials included well‐nourished populations (Blackwell 1973; Elwood 1981; Hunt 1976; Jahan 2013; Kafatos 1989; Oaks 2014; Ross 1985; Sweeney 1985; Viegas 1982a; Viegas 1982b).

Interventions

Five trials (Briley 2002; Hunt 1976; Jahan 2013; Kafatos 1989; Sweeney 1985) evaluated nutritional education to increase energy and protein intake. Twelve trials (Blackwell 1973; Ceesay 1997; Elwood 1981; Girija 1984; Huybregts 2009; Kardjati 1988; Mora 1978; Oaks 2014; Ross 1985; Rush 1980; Viegas 1982a; Viegas 1982b) assessed the impact of balanced energy/protein supplementation. Only one trial assessed the effects of high‐protein nutritional supplements (Rush 1980). Two trials (Viegas 1982a; Viegas 1982b) investigated the effects of isocaloric protein supplements. Interventions for nutritional education included counselling or classes versus no interventions (four trials: Hunt 1976; Jahan 2013; Kafatos 1989; Sweeney 1985) and counselling versus home visits without counselling (one trial: Briley 2002). Interventions for balanced energy and protein supplementation included supplementation versus control supplements (nine trials: Blackwell 1973; Huybregts 2009; Kardjati 1988; Mora 1978; Oaks 2014; Ross 1985; Rush 1980; Viegas 1982a; Viegas 1982b) and supplementation versus no intervention (three trials: Ceesay 1997; Elwood 1981; Girija 1984). Intervention for high‐protein nutritional supplements included supplementation versus supplement containing vitamins/minerals (Rush 1980). Intervention for isocaloric‐protein nutritional supplements included supplementation versus supplement of flavoured carbonated water containing iron and vitamin C (Viegas 1982a; Viegas 1982b).

Outcomes

Most of the trials focused on assessing the effects of dietary education, supplementation, or restriction on gestational weight gain, pre‐eclampsia and/or pregnancy outcomes, or child development.

Setting

Seven trials were from high‐income countries such as the USA and UK, and 10 trials from low‐ and middle‐income countries such as Gambia, Taiwan, India, Burkina Faso, Greece, Indonesia, Colombia, South Africa, Ghana and Bangladesh.

For details of the included studies, see the Characteristics of included studies table.

Sequence generation

Seven trials had a low risk of bias because of adequate randomisation of participants to the intervention groups (Elwood 1981; Huybregts 2009; Jahan 2013; Kafatos 1989; Kardjati 1988; Rush 1980; Sweeney 1985). For 10 trials, risk of bias could not be adequately judged because no detailed information was provided about allocation sequence generation (Blackwell 1973; Briley 2002; Ceesay 1997; Girija 1984; Hunt 1976; Mora 1978; Oaks 2014; Ross 1985; Viegas 1982a; Viegas 1982b).

Allocation concealment

Six trials had a low risk of bias through the use of sequentially numbered, opaque, sealed envelopes or drug containers of identical appearance or central allocation (Blackwell 1973; Elwood 1981; Huybregts 2009; Kafatos 1989; Kardjati 1988; Rush 1980). Eleven trials provided no information about allocation concealment (Briley 2002; Ceesay 1997; Girija 1984; Hunt 1976; Jahan 2013; Mora 1978; Oaks 2014; Ross 1985; Sweeney 1985; Viegas 1982a; Viegas 1982b).

Participants and personnel

One trial had a low risk of bias using double blinding (Blackwell 1973). Twelve trials had a high risk of bias owing to a lack of blinding. Four trials could not be judged for the risk because no information was provided (Kardjati 1988; Oaks 2014; Viegas 1982a; Viegas 1982b).

Outcome assessment

Three trials had a low risk of bias (Elwood 1981; Huybregts 2009; Rush 1980). Two trials had a high risk of bias due to the fact that delivery of the intervention and outcome assessment were carried out by the same personnel (Hunt 1976; Kafatos 1989). The other 12 trials were judged unclear due to no information provided about outcome assessors.

Primary outcomes

For the primary outcomes, there was no significant effect on stillbirth (risk ratio (RR) 0.37, 95% confidence interval (CI) 0.07 to 1.90; one trial, 431 women ‐ Analysis 1.1) or neonatal death (RR 1.28, 95% CI 0.35 to 4.72; one trial, 448 women ‐ Analysis 1.2). Perinatal mortality was not reported in any trials.

Secondary outcomes

There was a significant increase in birthweight among undernourished women (mean difference (MD) 489.76, 95% CI 427.93 to 551.59; two trials, 320 women; I² = 0%), although there was no significant increase among adequately nourished women (MD 15.00, 95% CI ‐76.30 to 106.30; one trial, 406 women) in the subgroup analysis (subgroup differences P < 0.0001) (Analysis 1.3). There was no significant difference in birth length (Analysis 1.4), and small‐for‐gestational age (Analysis 1.6). The results of total gestational weight gain (Briley 2002; Kafatos 1989) were inconsistent and showed higher heterogeneity (I² = 63%) (Analysis 1.12). In Jahan 2013, total body weight gain from seven to nine months was significantly increased in the intervention group compared to control group (8.6 ± 2.3 kg versus 5.4 ± 2.3 kg) among poor urban women in Bangladesh (data not shown in the forest plot). Birth head circumference (cm) was significantly increased in the intervention group (MD 0.99 cm, 95% CI 0.43 to 1.55; one trial, 389 women ‐ Analysis 1.5). The 'significant' reduction in preterm birth associated with education (RR 0.46, 95% CI 0.21 to 0.98, P < 0.05; two trials, 449 women ‐ Analysis 1.7) was not consistent with the total absence of effect on mean gestational age (MD ‐0.10 weeks, 95% CI ‐0.48 to 0.28; one trial, 399 women ‐ Analysis 1.8).

Sensitivity analyses (Figure 1) was conducted to explore different values of the ICC used for adjustments of data from the cluster trial, Kafatos 1989. Using different values for the ICC, the risk became non‐significant when the ICC was more than 0.01; however, overall results did not qualitatively change the relative risks for preterm in Kafatos 1989.

Antenatal nutritional education was associated with a significant reduction in low birthweight (RR 0.04, 95% CI 0.01 to 0.14; one trial, 300 women; Analysis 1.9). Within the methodological limitations discussed above, education to increase protein intake seems to be successful in achieving its goal (protein intake: MD +6.99 g/day, 95% CI 3.02 to 10.97, P < 0.05; three trials, 632 women ‐ Analysis 1.10), but there was no significant increase in energy intake (energy intake: MD +105.61 kcal/day, 95% CI ‐18.94 to 230.15, P = 0.10; three trials, 342 women ‐ Analysis 1.11).

Primary outcomes

Providing balanced energy and protein supplementation significantly reduced the risk of stillbirth (RR 0.60, 95% CI 0.39 to 0.94; five trials, 3408 women ‐ Analysis 2.1). Neonatal death was unaffected (RR 0.68, 95% CI 0.43 to 1.07; five trials, 3381 women ‐ Analysis 2.2).

Sensitivity analysis was conducted to explore different values of ICC used for adjustments of data from the cluster trial, Ceesay 1997. Sensitivity analyses (Figure 2) for ICCs of 0.02 to 0 made little difference; using values of 0.01 for the ICC did not qualitatively change the relative risks for stillbirth in Ceesay 1997. We also conducted the analysis using ICC = 0.02 for risk of stillbirth (RR 0.62, 95% CI 0.39 to 0.99), but this did not change the overall risk.

Secondary outcomes

Supplementation was also associated with significant increases in mean birthweight (random‐effects MD +40.96 g, 95% CI 4.66 to 77.26, Tau² = 1744, I² = 44%, P = 0.03; 11 trials, 5385 infants ‐ Analysis 2.3 , funnel plot Figure 5). Although clinically small, no statistically significant difference (random‐effects MD 0.18, 95% CI ‐0.04 to 0.40; five trials, 3370 women; I² = 44% ‐ Analysis 2.4) was observed in birth length (cm), and also no significant difference was found for birth head circumference (Analysis 2.5). The incidence of small‐for‐gestational age birth was significantly reduced (RR 0.79, 95% CI 0.69 to 0.90, I² = 16%; seven trials, 4408 women ‐ Analysis 2.6). There were no significant effects observed on preterm birth (Analysis 2.7), gestational age (week) (Analysis 2.8), or weekly gestational weight gain (g/week) ((MD 18.63, 95% CI ‐1.81 to 39.07, I² = 57%; Nine trials, 2391 women, Analysis 2.9, funnel plot Figure 6). The rather meagre data on pre‐eclampsia did not suggest a reduction in risk with supplementation (RR 1.48, 95% CI 0.82 to 2.66; two trials, 463 women ‐ Analysis 2.10). The funnel plots (Figure 5; Figure 6) did not show any publication bias.

Although postnatal follow‐up was limited to a small number of trials, the enhancement of fetal growth observed in those trials was not reflected in larger size or improved neurocognitive development at one year. The Bayley mental score at one year had no significant effect in one trial (Rush 1980; Analysis 2.11). The Taiwan trial (Blackwell 1973) detected no effect on the Stanford‐Binet IQ score at five years (Analysis 2.12), and weight at one year (Analysis 2.13). As the data of the standard deviation of length at one year for Blackwell 1973 were not credible compared with the Rush 1980 study, we omitted the former from the analysis and only showed the data from Rush 1980 (Analysis 2.14). There was no significant effect on head circumference at one year from either the Taiwan (Blackwell 1973) or Harlem trials (Rush 1980) (Analysis 2.15). Mortality from birth to age 12 months follow‐up showed no significant difference between prenatal lipid‐based nutrient supplements versus prenatal multiple micronutrients (Huybregts 2009) (RR 1.10, 95% CI 0.58 to 2.10; one study, 1023 women; Analysis 2.17). A follow‐up study at age 12 months of Huybregts 2009 showed no significant difference for infant growth (length for age growth, weight per month, length per month, head circumference per month, chest circumference per month), mortality, or morbidity between groups (Lanou 2014).

Maternal outcomes other than weight gain were reported infrequently. Only two trials reported results on other outcomes. The Bogota trial (Mora 1978) detected no significant reduction in duration of labour with supplementation (Analysis 2.16). The East Java trial (Kardjati 1988) found no increase in maternal weight at four weeks postpartum (Analysis 2.18).

In this update, we found one trial of 1320 pregnant women for lipid‐based nutrient supplementation (only the conference abstract was available). However, we could not incorporate this trial in the meta‐analysis as the only outcome was maternal salivary cortisol at 36 gestational weeks (Oaks 2014).

Follow‐up at 6.5 to 9.5 years of age for approximately 25% of the children randomised in Ceesay 1997 found no difference in immune function (delayed‐hypersensitivity skin tests, antibody responses to pneumococcal and rabies vaccines, and salivary IgA concentration) between the intervention and control groups (data not shown in data and analysis table). Follow‐up at 11 to 17 years of age for approximately two‐thirds of the children who were still alive found no significant differences in height (Analysis 2.19), weight (Analysis 2.20), or systolic or diastolic blood pressure (data not shown), but did find a small increase in the mean BMI z‐score (MD +0.16, 95% CI +0.01 to +0.31; one trial, 855 children ‐ Analysis 2.21) in the control group. However, the difference in BMI was in contrast with the absence of the effect on per cent body fat (Analysis 2.22). Follow‐up at 16 to 22 years of age of Ceesay 1997 showed no evidence (data not shown) that maternal protein‐energy supplementation during pregnancy compared with supplementation during lactation (controlled group were supplemented protein‐energy during lactation) affected the cognitive ability or school performance of offspring in rural Gambia (Alderman 2014).

In a follow‐up study of offspring at the mean age of 22 to 23 years (Viegas 1982a), 236 (83%) offspring were traced and 118 (50%) were assessed as being at risk of cardiovascular and metabolic disease; however, nutritional supplementation (protein/energy/vitamins; energy/vitamins or vitamins only) showed no strong association (data not shown) with any markers of adult disease risk in either unselected or undernourished mothers (Macleod 2013).

Primary outcomes

For primary outcomes, the Harlem trial (Rush 1980) reported non‐significant effects in stillbirth (RR 0.81, 95% CI 0.31 to 2.15; one trial, 529 women ‐ Analysis 3.1) and neonatal death (RR 2.78, 95% CI 0.75 to 10.36; one trial, 529 women ‐ Analysis 3.2) with high‐protein supplementation.

Secondary outcomes

The only available trial (Rush 1980) provided evidence of significant increases in infants born small‐for‐gestational age (RR 1.58, 95% CI 1.03 to 2.41, P = 0.04; one trial, 505 women ‐ Analysis 3.3), although there was no significant effect for birthweight ((MD ‐73.00, 95% CI ‐171.26 to 25.26, I² = 0%, one study, 504 women, Analysis 3.4) or preterm birth (RR 1.14, 95% CI 0.83 to 1.56, I² = 0%, one study, 505 women, Analysis 3.5).

High‐protein supplementation had no effect on weekly gestational weight gain (MD +4.50 g/week, 95% CI ‐33.55 to +42.55; one trial, 486 women ‐ Analysis 3.6). At one‐year follow‐up in the Harlem trial (Rush 1980), high‐protein supplementation was not associated with detectable differences in weight (Analysis 3.7), length (Analysis 3.8), head circumference (Analysis 3.9) or Bayley mental score (Analysis 3.10).

Primary outcomes

Primary outcomes were not reported.

Secondary outcomes

Owing to the significant heterogeneity in the results for birthweight and gestational weight gain, the data were pooled using a random‐effects model. There was no significant effect on birthweight or gestational weight gain of isocaloric protein supplementation. For mean birthweight the MD was +108.25 g (95% CI ‐220.89 to 437.40, Tau² = 47211, I² = 84%; two trials, 184 infants ‐ Analysis 4.1), while for gestational weight gain, the MD was +110.45 g/week (95% CI ‐82.87 to 303.76, Tau² = 16542, I² = 85%; two trials, 184 women ‐ Analysis 4.2).