The effectiveness of interventions to treat severe acute malnutrition in young children: a systematic review

Summary of quality assessment

The methodological rigour of the trial by Akech and colleagues49 was rated moderate overall (Table 10). The trial was potentially at risk of selection bias, because not all of the eligible children who were selected actually participated in the trial either for clinical reasons or because consent was declined. The study was a RCT and an adequate method (use of sealed envelopes) was used for randomisation to treatment groups, resulting in a strong rating for study design. Baseline characteristics and disease severity indices were reported to be balanced across the three fluid intervention arms (although data were not presented for the HAS arm because of small numbers), also leading to a strong rating. However, neither the participants nor the care providers were blinded to treatment and no details were reported regarding the outcome assessors, leading to a higher risk of detection bias and thus a weak rating. For data collection methods, the trial was rated as moderate as it used valid criteria for measuring shock, but it was not possible to judge whether or not these criteria were reliable. There were no dropouts or withdrawals from the trial, only losses because of deaths, and all surviving children completed the study, indicating a low risk of attrition bias. The intervention integrity of the trial was strong as all the participants were deemed likely to have received his or her allocated intervention without any cross-contamination. Appropriate statistical methods were employed in the data analysis and the authors report that all analyses were performed using the intention-to-treat (ITT) principle, although outcomes were presented for all survivors (those who died were not included), rather than for all those randomised. However, the area under curves (AUCs) were calculated in order to compensate for the confounding effect of mortality and, hence, missing observations, leading to biases in the highest risk group and resulting imbalance within the survivors. It should also be noted that the trial was prematurely terminated because of the high overall mortality and inadequate correction of shock in all study arms after an interim review of safety data and consultation with the external safety monitors. As a result, the study did not recruit the required sample size and was therefore underpowered.

Mortality

Overall mortality was high, with 51% (31/61) of children not surviving. Of these deaths, 39% (12/31) occurred within 24 hours of recruitment,49 whereas 52% (16/31) of fatalities occurred within 48 hours of enrolment (Professor Kathryn Maitland, Imperial College London, 2011, personal communication). There was no statistically significant difference in mortality rates between the three treatment groups (p = 0.62), nor between children who received RL versus HSD/5D (p = 0.34) (Table 11). On Kaplan–Meier survival analysis, there was no significant difference in time to death when any of the intervention fluids were used for resuscitation (log-rank test combined, p = 0.42).

Mortality rates within a number of subgroups were also reported by Akech and colleagues,49 although not all were presented as comparisons between fluid resuscitation treatment groups. In those with severe diarrhoeal shock, mortality was higher in the standard HSD/5D group than in the RL group {13/19 (68%) vs 9/22 (43%), respectively; p = 0.11 [note: there is a possible error reported in the publication, RL should be 9/21 (43%)]}, although the opposite trend was observed for those with presumptive (non-diarrhoeal) shock [2/7 (29%) vs 4/8 (50%), respectively; p = 0.61 (note: there is a possible error reported in the publication for presumptive shock for HSD/5D)], but neither difference reached statistical significance. Children who fulfilled the WHO malnutrition shock definition at admission were at a statistically significant increased risk of death [risk ratio (RR) 2.0, 95% confidence interval (CI) 0.92 to 4.36; p = 0.05] compared with those who did not fulfil this definition, irrespective of allocated intervention. Similarly, kwashiorkor was associated with an increased risk of death irrespective of treatment arm [odds ratio (OR) 2.2, 95% CI 0.7 to 10.1; p = 0.14], though this was not statistically significant. Mortality in children who were HIV+ve was similar to those that among who were HIV–ve (42% vs 45%, respectively; p-value not reported) and infection with HIV did not significantly increase the risk of death (OR 1.18, 95% CI 0.38 to 3.72; p = 0.76).

Weight gain and anthropometry

Weight gain and anthropometry outcomes were not reported by the Akech and colleagues’ trial49 because of the focus of the study (i.e. the trial was designed to look at emergency management of shock rather than nutritional rehabilitation).

Resolution of shock

The proportion of children in whom shock persisted after fluid resuscitation treatment was considerable, but was not significantly different between RL and HSD/5D at either 8 or 24 hours (Table 12). The authors report that a larger decline in the proportion with shock was observed in children who received RL than in those who received HSD/5D, particularly in the diarrhoeal group, but the differences were not significant at any time point (data not shown).

Oliguria

Adequate urinary output was used as a gold standard for successful fluid resuscitation, with oliguria (the production of an abnormally small volume of urine) being a marker of persistent, severe shock. The incidence of oliguria was significantly higher in children receiving the standard WHO HSD/5D solution than in those receiving RL at 8 hours (reported by the authors as p = 0.02 in the table, but p = 0.05 in the text). This trend was also evident at 24 hours, but was no longer statistically significant (p = 0.16) (Table 13).

In an additional analysis, the median AUC for the hourly urine output was significantly lower in HSD/5D participants (51 ml/kg/hour, IQR 36–116) than in RL participants (101 ml/kg/hour, IQR 63–141; Kruskal–Wallis chi-squared = 4.6; p = 0.03) (data not shown).

Tachycardia

Persistent tachycardia is an index of unresolved shock and was defined as a heart rate of > 160 beats/minute. Children who received the standard WHO HSD/5D solution had a higher incidence of tachycardia (and hence unresolved shock) compared with those who received the RL solution, becoming statistically significant at 24 hours (p = 0.04) (Table 14).

In the additional analysis, median AUC of heart rates were similar for both treatments (Kruskal–Wallis chi-squared = 0.3; p = 0.59).

Adverse events

Although the incidence of adverse events was not presented, Akech and colleagues49 did report that no child developed clinical features of pulmonary oedema or allergic reaction (to HAS) during the course of study observation. In addition, no diuretics were required or prescribed during the trial and there were no differences in the mean sodium concentration at admission (133 ± 11 mmol/l vs 134 ± 10 mmol/l, respectively; p = 0.81), 8 hours (134 ± 10 mmol/l vs 139 ± 10 mmol/l, respectively; p = 0.09) or 24 hours (138 ± 9 mmol/l vs 140 ± 9 mmol/l, respectively; p = 0.47) between those who received HSD/5D and RL implying that children did not exhibit the problem of either water or sodium retention.

Other outcomes

Additional outcomes such as severe tachypnoea (rapid breathing of > 60 breaths/minute), creatinine levels and resolution of base deficit (acidosis) were also reported in the trial publication, but have not been presented here. Further details are available in the data extraction forms in Appendix 8.

Summary

• Only one trial49 was identified that evaluated the efficacy of fluid resuscitation solutions for the treatment of children with SAM and hypovolaemic shock. The trial was relatively small and was rated as having a moderate methodological quality overall. It should be noted that the study was underpowered because of premature termination of the trial because of safety issues (i.e. high overall mortality and inadequate correction of shock in both arms) and the results should therefore be interpreted with caution.

• The overall mortality rate in the trial was high (> 45%), with no statistically significant differences between treatment groups nor any difference in the time to death between treatment arms. There was an inadequate correction of shock that persisted after fluid resuscitation treatment in both the standard WHO HSD/5D hypotonic solution and the isotonic RL solution groups (> 50%).

• The incidence of oliguria (used as a marker of persistent, severe shock) was higher in children receiving HSD/5D hypotonic solution than in those receiving RL, being significant at 8 hours, but not at 24 hours. Similarly, children who received the HSD/5D solution had a higher incidence of tachycardia (denoting unresolved shock) than those in the RL group, becoming statistically significant at 24 hours.

• The isotonic RL solution was found to be as safe as the currently recommended WHO HSD/5D hypotonic solution with no adverse events reported. However, it should be noted that all the fluid solutions were deemed inadequate by the authors in the correction of shock.

Summary of quality assessment

The methodological quality and the quality of reporting of the five included trials did not vary greatly. Two trials50,51 were rated strong overall, with the other three trials being rated moderate54,55,57 (Table 16).

Selection bias varied between the studies, with three trials50,54,55 being at potential risk of selection bias. For all of these trials, it was unclear what proportion of selected individuals agreed to participate in the trials before they were randomised. In addition, the included children in both trials by Dutta and colleagues54,55 were considered to be only somewhat likely to be representative of the target population, leading to a higher risk of selection bias. Conversely, the study design of all five trials was strong, with all being RCTs and using an adequate method to generate random allocations. Hence, trial arms within all the studies were balanced with respect to baseline characteristics and confounders, leading to a strong rating. All but one57 trial employed a double-blind method, reporting that the interventions looked identical to participants. Alam and colleagues57 reported that treatments could not be blinded to those involved in the study because of visible differences in the three ORS solutions. Furthermore, neither study by Alam and colleagues51,57 reported sufficient details on the blinding of outcome assessors and they were therefore rated as moderate51 and weak57 as this could lead to detection bias. For data collection methods, all five trials were rated as moderate as they included valid data collection tools, but it was not possible to judge if these tools were reliable.

Sources of attrition bias in clinical trials include losses of participants to follow-up, unequal dropout rates between interventions, selective reporting of outcomes (missing outcomes) and failure to explain why participants are missing (e.g. whether or not they are missing at random). All five trials were rated as strong for withdrawals and dropouts, though they varied in their level of reporting. One trial50 provided both the number and reasons for any losses and had 80–100% of participants completing the study, indicating a low risk of attrition bias. Three trials51,54,57 either did not report any information on dropouts or only reported numbers (without reasons), but had most or all the participants completing the study. Consequently, these were rated as strong as the outcomes can be considered to be reasonably reliable and reflect the study population. In the trial by Dutta and colleagues,55 two contrasting ratings were allocated because all participants completed the acute phase of the study up to the point of recovery (rated strong), but over half the participants were not included in the 30-day follow-up assessments and neither the number nor reasons for the dropouts were reported by the authors (rated weak). The intervention integrity of all five trials was strong, as all the participants were deemed likely to have received their allocated intervention without any cross-contamination. All five trials used appropriate statistical methods in their analysis, although two51,57 did not perform an ITT analysis. For Alam and colleagues,51 this was presumably because the children with SAM were only a subgroup of the total study population. It should be pointed out that all five studies excluded children with severe infections, and as this is not uncommon in hospitalised children with SAM (Professor Kathryn Maitland, Imperial College, London, 2011, personal communication), the results of the studies may not be generalisable to most children with SAM and acute diarrhoea.

Mortality

The two studies by Alam and colleagues50,57 were the only trials to report mortality, with no deaths in any treatment group (Table 17). The other trials did not report this outcome, although in the third Alam and colleagues trial51 it is assumed there were no deaths as the children who were not discharged (after having recovered) were accounted for as dropouts. In both trials by Dutta and colleagues,54,55 it remains unclear whether the few children who did not recover within the 5 days of hospitalisation were lost to follow-up or died as no details were reported.

Weight gain

Most of the trials51,54,55,57 reported weight gain as an outcome measure, with two finding significant differences between treatment groups (Table 18). Dutta and colleagues54 found that children receiving the standard WHO/UNICEF-ORS had at discharge gained significantly more weight (p = 0.001) than those receiving the H-ORS (or on day 5 if they did not recover during this period). However, in the Alam and colleagues trial51 weight gain was similar in the H-ORS and WHO-ORS treatment groups. Alam and colleagues57 reported that children receiving the rice-ORS had significantly greater weight gain at 72 hours than those receiving either of the glucose-ORS treatments (p = 0.05). There was no statistically significant benefit on weight gain from a zinc supplement compared with placebo either at the time of recovery or at 30 days follow-up in the trial by Dutta and colleagues. 55 Alam and colleagues50 did not provide any numerical data on weight gain, but stated that weight gain before discharge was similar between the groups.

Duration of diarrhoea

The length of time that diarrhoea persisted in treated children was reported in four51,54,55,57 of the five trials and can be seen in Table 19. The two trials51,54 evaluating a hypo-osmolar-ORS found similar results. The duration of diarrhoea was statistically significantly shorter in children who received the H-ORS than in those who received the standard WHO/UNICEF-ORS (41.5 vs 66.4 hours, respectively; p = 0.001). 54 In the Alam and colleagues trial,51 the duration of diarrhoea was reported separately for a rehydration phase and maintenance phase (as well as overall duration), though the timescale for these phases was not defined. The difference between treatment groups followed the same pattern and was statistically significant during the maintenance phase in favour of H-ORS (95% CI 0.46 to 0.88; p = 0.007), but was no longer significant when the phases were combined as overall duration. Supplementation with zinc was favourable compared with placebo with a mean difference in duration of diarrhoea of approximately 30 hours (p = 0.0001),55 whereas in another study,57 although the median duration of diarrhoea was lower in the rice-ORS group than in the glucose-ORS or glucose-ORS + ARS groups, this did not reach statistical significance.

Frequency of diarrhoea

The frequency of diarrhoea was reported by three trials,51,54,57 although differences in the way this outcome was reported make direct comparisons between trials difficult. Alam and colleagues51 reported the number of stools in a 4-hour period, whereas the other two trials54,57 reported stool output (g/kg and ml/kg, respectively) in several 24-hour periods and also at recovery54 (Table 20). Despite differences in the reporting, for both studies evaluating H-ORS,51,54 the mean frequency of stool output was significantly less in the children receiving H-ORS than in those receiving standard WHO-ORS at all time points. For the third trial, by Alam and colleagues,57 the cumulative mean stool output of children receiving rice-ORS was statistically significantly lower than among children receiving glucose-ORS at 24 hours (32% mean reduction, 95% CI 44% to 174%; p = 0.004), and this statistical difference was maintained at 48 and 72 hours. Compared with the study by Dutta and colleagues,54 data for stool output per kg of body weight were markedly higher in the trial by Alam and colleagues,57 but the reason for this is unclear.

Recovery

Two54,55 of the five trials specifically reported recovery (proportion of children who recovered within 5 days) as an outcome (Table 21), with one of these54 also reporting median survival time to recovery. Recovery was defined as the passage of a normal stool or no stool for the last 18 hours,55 or was assumed to be when diarrhoea had ceased (two formed stools passed or no stool for 12 hours). 54 A further two trials50,57 reported outcomes that inferred recovery in the children. Alam and colleagues57 reported the time taken to attain an oedema-free W/L of 80% of the NCHS median, whereas Alam and colleagues50 reported the number of children who were adequately rehydrated at 12 hours.

Dutta and colleagues55 found a small but significant (p = 0.04) difference between treatment groups with all children supplemented with zinc recovering within 5 days of hospitalisation, compared with 89% of children receiving placebo. Dutta and colleagues54 also reported a high recovery rate, with all but three children (all in WHO-ORS group) having recovered within 5 days of treatment, but the difference between treatment groups was not significant. However, children treated with H-ORS recovered significantly quicker than those treated with the WHO-ORS (36 vs 53 hours, respectively; p = 0.001).

In the Alam and colleagues57 trial, it took around 7 days for children to attain an oedema-free W/L of 80%, being similar regardless of the type of ORS (p = 0.99).

In the Alam and colleagues trial,50 most of the children in both treatment arms were adequately rehydrated at 12 hours, with no statistically significant differences between groups.

Consumption of oral rehydration solution

Most of the trials51,54,55,57 measured how much ORS was consumed by the children, either as the total amount consumed (litres)51,55 or as ml/kg of body weight54,57 (Table 22). In two trials,51,54 children receiving H-ORS needed to consume less rehydration solution than those receiving the standard WHO-ORS, although this reached statistical significance in only one of the trials (p = 0.0001). 54 The other two studies also found significant differences in favour of the intervention groups. Dutta and colleagues55 reported a lower ORS consumption in children supplemented with zinc than in those supplemented with placebo (p = 0.0001). Alam and colleagues57 found that children receiving rice-ORS had a significantly lower ORS intake at 18 hours compared with those receiving glucose-ORS (see Appendix 9). This difference was maintained at each 6-hourly interval thereafter until 72 hours, when there was a 38% reduction in intake (p = 0.012).

Adverse effects

Adverse effects were not reported in any detail by the included studies. Two trials51,55 did not report any safety issues, whereas two trials54,57 reported that no children developed symptoms of overhydration. Alam and colleagues50 report that prevention of overhydration is the primary theoretical advantage of ReSoMal. Overhydration was defined as a weight gain > 5% after correction of dehydration at any time during the study period with any of the following signs: periorbital oedema/puffy face, increased heart rate (> 160/minute) or increased respiration (> 60/minute). Although there appeared to be a lower occurrence of over-rehydration in those children who received ReSoMal than in those receiving WHO-ORS, numbers were small and this was not supported statistically (Table 23). Alam and colleagues50 also looked in detail at serum electrolytes and, thus, the incidence of hypo- and hyperkalaemia and hypo- and hypernatraemia (these outcomes have not been reported here as they are not main outcomes of interest to this review, but data are available in Appendix 9). However, it is worth noting that three children in the ReSoMal group developed severe hyponatraemia (low serum sodium) by 24 hours, with one child having a resulting convulsion, which the authors highlight as a safety concern that may limit the use of ReSoMal in its current formulation.

Summary

• Five trials evaluated the treatment of children with acute diarrhoea with various types of ORS, including a H-ORS,51,54 a modified WHO-ORS (ReSoMal),50 an ORS containing either glucose, glucose plus ARS or rice powder,57 and supplementation with zinc. 55 The trials were all of strong or moderate methodological quality.

• There were no deaths in the two trials that reported mortality,50,57 and it is assumed that there were no deaths in a third trial,51 as all children who did not recover were accounted for as dropouts.

• Compared with the standard WHO-ORS, children receiving the H-ORS had a significantly shorter duration and lower frequency of diarrhoea, consumed less ORS and had a quicker time to recovery (one trial54).

• There appeared to be no benefit from H-ORS with respect to weight gain compared with WHO-ORS.

• Supplementation with 40 mg elemental zinc (as zinc syrup) in addition to a standard WHO-ORS resulted in a significantly shorter duration of diarrhoea, a better recovery rate and a lower ORS intake, but no difference compared with placebo in terms of weight gain. 55

• Rice-ORS appeared to be more favourable than glucose-ORS in treating children with cholera diarrhoea. The rice-ORS groups had significantly better weight gain, a lower frequency and duration of diarrhoea and consumed less ORS. 57

• ReSoMal did not appear to show any advantage over a standard WHO-ORS in rehydrating severely malnourished children with acute diarrhoea, although it was beneficial in correcting potassium depletion.

• Adverse effects were not generally reported by the trials, although ReSoMal50 may result in symptomatic severe hyponatraemia and seizures in some patients.

Summary of quality assessment

Two of the included trials were rated overall as ‘weak’ for their methodological quality and quality of reporting (Table 25),52,53,58 with the third being rated overall as ‘strong’. 56

Trials were rated as moderate,52,58 weak53 or strong56 for selection bias. A moderate rating indicates that the selected individuals are at least somewhat likely to be representative of the target population and at least 60% of selected individuals participated in the trial. A weak rating indicates that participants may not be representative of the target population, or that the selection method and/or levels of participation were not described. The two trials with moderate and weak ratings were at potential risk of selection bias. 52,53,58 All three trials were rated as strong for their study design (RCTs).

There were no important differences in baseline characteristics between the trial arms, and without potentially confounding variables all three trials were rated as strong. For blinding, only one trial employed a double-blind method and was therefore rated as strong. 56 Of the other two trials, both were rated as weak, with one employing a single-blind method52,58 and the other reporting no details. 53 It is recognised that blinding of children is not always possible because of the nature of the intervention. This could lead to bias in either the care provided (performance bias) or how the outcomes were assessed (measurement or detection bias), or both. Not blinding children/parents to the research question could lead to reporting bias. Although it may be problematic in some circumstances to blind children/parents to the intervention, the potential bias it can introduce needs to be kept in mind when interpreting the results.

For data collection methods, two trials were rated as moderate. 53,56 Although both trials included valid data collection tools, it was not possible to judge if these tools were reliably employed. The remaining trial was rated as weak, as it was not possible to assess if the data collection tools were either valid or shown to be reliable. 52,58 One trial52,58 provided both numbers and reasons for withdrawals and dropouts, and with a follow-up rate of ≥ 80% received a strong rating. Of the remaining two trials,53,56 both had lower follow-up rates (60–79%) and one provided inadequate information by giving reasons for withdrawal, but not numbers for each group. 53 There was a possible risk of attrition bias in both these trials and they both received an overall rating of moderate for withdrawals and dropouts. For the section of the tool capturing intervention integrity, two trials52,56,58 reported that > 80% of the participants received the intervention, and in the third53 60–79% received the intervention. The consistency of the intervention was measured by all three trials, using weight gain as the measure, and there appeared to be no contamination of the interventions (i.e. all children received the allocated diet only). All trials used patients as the unit of allocation and analysis for statistical analysis of the results, and were judged to use appropriate methods of statistical analysis for the research question. Two of the trials did not perform an ITT analysis,52,56,58 and it was not possible to determine how missing data were dealt with in the analysis in the third trial. 53

Mortality

Only Amadi and colleagues52,58 reported mortality as an outcome (Table 26). Although mortality was highest in the Neocate group (22/100), the difference was not statistically significant (see Table 26). The highest number of deaths for the combined treatment groups (43%) occurred in the second treatment week (week 1 = 31%, week 3 = 26% and week 4 = 10%). Irrespective of treatment arm, death was more likely to occur in children with marasmic kwashiorkor (34.9%; p = 0.004), or cryptosporidiosis (no data reported) and in children identified as HIV+ve (24% compared with 11% of HIV–ve children; p = 0.04). Although mortality was not formally identified as an outcome in the trial by Nurko and colleagues,56 the authors reported that five children died during the trial and how many deaths occurred in each group (see Table 26). However, the causes of death, intestinal pneumatosis (n = 2), central line-associated sepsis (n = 2) or bacterial sepsis (n = 1), were reported only for the whole trial population and not by group. Bhutta and colleagues53 also did not specify mortality as an outcome; however, it can be assumed that there were no deaths, because all children either completed the treatment or were accounted for as dropouts.

Weight gain

Measures of weight gain were employed by all three trials; however, only one trial reported weight gain relative to initial weight (the benefit of relative weight gain measures is that any effects because of starting differences in body weight are removed). In the trial by Amadi and colleagues,52,58 feeding with Neocate was associated with a 41% better gain in weight from nadir compared with the skimmed milk/soy-based diet, and the difference was statistically significant (p = 0.002) (Table 27). In the trial by Bhutta and colleagues,53 weight gain was higher for the intervention diet of soy than for KY milk, but reached statistical significance only at the end of treatment (i.e. week 2; p < 0.02). Conversely, mean daily weight gain was higher in the KY milk group, but the difference between groups was not statistically significant. It should be noted that there was also a reported weight loss in two children in the soy group (10%) and seven (37%) in the KY milk group (p = not statistically significant). Nurko and colleagues56 reported statistically significant weight gains for all three diets used in their trial for their comparison of weight change from admission versus at the end of the protocol and from admission versus discharge. However, no statistically significant differences between the three treatment arms were reported.

Anthropometry

Two of the studies reported anthropometry outcomes as well as weight gain. Amadi and colleagues52,58 reported that increases in z-scores of W/A and W/H were statistically significantly higher from admission (W/A, p = 0.018; W/H, p < 0.001) and from nadir (W/A, p = 0.002; W/H, p < 0.001) for the Neocate group, with results mirrored in HIV+ve (W/A, p = 0.007; W/H, p < 0.001) and HIV–ve (W/A, p = 0.01; W/H, p = 0.009) subgroups (Table 28). In the trial by Bhutta and colleagues,53 increases in W/A z-score during the study were significantly greater in the soy group (p < 0.001) than in the KY milk group (p = not statistically significant), but no statistical comparison between the groups was reported. Bhutta and colleagues53 did report a statistical comparison between the groups for improvement in mid-arm circumference, which was significantly higher in the soy intervention group (1.0 cm vs 0.1 cm; p < 0.001).

Diarrhoea

Diarrhoea output was quantified either by collecting urine separately from stools (using adhesive urine bags and pre-weighed nappies/diapers)53 or by the use of metabolic beds/cots for separation of stool from urine. 56 There were no statistically significant differences in any of the measures of diarrhoea between treatment arms in the two trials53,56 that reported these outcomes (Table 29). In addition, Amadi and colleagues,52,58 who presented no numerical data, stated that there were no differences in either stool number or frequency.

Oral rehydration solution intake

Only Bhutta and colleagues53 reported ORS intake, which was significantly reduced by week 2 in the soy intervention arm compared with the KY milk diet (p < 0.05); however, differences in time to recovery were not statistically significant between the two diets (Table 30).

Calorie intake

Surprisingly, Amadi and colleagues52,58 reported that intake of calories (per kg per day) as liquid feeds, was statistically significantly higher at all time points for the control group (p < 0.0001). However, it should be noted that in addition to the liquid feed based on skimmed milk, the control group also received soy-based porridge from the beginning of the second week. In contrast, Bhutta and colleagues53 found caloric intake (per kg per day) to be only significantly higher for the soy-based intervention arm than for the KY milk arm at the end of week 1 (p < 0.02), and although this remained higher, it was no longer statistically significant at the end of week 2. Caloric intake in the trial by Nurko and colleagues56 was similar in all three diet groups (Table 31).

Treatment success/failure

Although clinical failure appeared to be lower in the soy-based diet arm than in the KY milk arm (no p-value reported), Bhutta and colleagues53 reported no statistical difference between treatment arms. Nurko and colleagues56 reported that there was no statistically significant differences between the three diets in terms of successful outcome (Table 32), with nutritional recovery and treatment failures appearing similar between the groups (p-values not reported). However, across the whole trial population (i.e. analysis not per treatment group), significant differences between treatment success and failure (p < 0.05) were associated with albumin and sodium concentration at admission, as well as the incidence of associated infections. Treatment failures were associated with formula intolerance (Table 33). Of the 15 treatment failures that occurred (see Table 32), 10 were successfully managed. One of the failures in the Nursoy group was because of allergy to the formula. The other five children who failed treatment died (see Table 26).

Safety outcomes

Only the study by Nurko and colleagues56 reported on safety, but there was no statistically significant difference in formula intolerance between the treatment arms (see Table 33). Of those children with formula intolerance, 15 were treatment failures (see Table 32) and four had intestinal pneumatosis (two of those with intestinal pneumatosis died; see Table 26).

Additional outcomes

Additional reported outcomes, such as protein ingested after full diet tolerance or time from diet start to failure, were reported in some studies, but have not been presented here. Further details can be seen in the data extraction forms in Appendix 9.

Summary

• Three trials52,53,56,58 evaluated the treatment of children with persistent diarrhoea, with each trial comparing different diets. The overall methodological quality was rated as weak for two trials52,53,58 and strong for one trial. 56

• Although all three trials employed a hospital inpatient setting, making diet intake easier to control and regulate, all three trials were judged to be open to a potential risk of bias in a number of areas and results should therefore be treated with caution.

• There were no significant differences in mortality rates between the diets employed in the two trials reporting mortality. 52,56,58

• None of the diets in the three included trials52,53,56,58 pertaining to children with persistent diarrhoea produced statistically significant improvements in measures of diarrhoea.

• The majority of diets appeared to be effective in increasing weight, with two out of three trials reporting better results for the diet used in the intervention arm. In the trial by Amadi and colleagues,52,58 Neocate produced greater weight gain over a 4-week period than the standard skimmed milk/soy-based diet, which was reflected by increases in W/A and W/H z-scores, as well as weight increases in both HIV+ve and HIV–ve subgroups. The full-strength soy diet in the trial by Bhutta and colleagues53 also produced better weight gain over a 2-week period than the half-strength buffalo milk diet with rice-lentils and yoghurt given to the control group. This was again reflected by increases in W/A z-scores. In contrast, the three diets of chicken, Nursoy and Vivonex (control) employed by Nurko and colleagues56 were found to be equally effective for weight gain.

Summary of quality assessment

Although 230 participants were randomly allocated to the ceftriaxone group, two of these were secondarily excluded; thus, only 228 were included in the analyses. The authors state that an ITT analysis was conducted, given that all children who had received at least one dose of the study drug were included. However, because of the post-randomisation exclusion of two participants, this was judged not to be a full ITT analysis during quality assessment.

Dubray and colleagues’ study59 was rated moderate in terms of its overall methodological quality, as shown in Table 35. More than 80% of the selected individuals, who are very likely to be representative of the target population, participated in the RCT. The use of a computer-generated block randomisation method and sealed envelopes for allocation was appropriate. Additionally, there were no important baseline differences between groups and the number and reasons for withdrawals and dropouts were reported per group. Therefore, this study was considered strong regarding the selection bias, study design, confounders and the withdrawals and dropouts components of quality assessment. Despite using valid data collection tools, the reliability of the tools is not reported, and, hence, the study strength on data collection methods was rated moderate. For the blinding component, the study was judged to have weak methodological strength because neither outcome assessors nor participants were blinded. Considering that the consistency of the intervention was measured, that 60–79% of the participants received the allocated intervention and that they are not likely to have received an unintended intervention, the intervention integrity is considered to have been ensured. Furthermore, the analysis performed was found to be appropriate for the study design, despite the shortcomings of the ITT analysis.

Mortality

Dubray and colleagues59 reported several mortality-related secondary outcomes, based on an analysis that excluded two participants who had been randomised, but who did not receive any treatment. As can be seen in Table 36, fewer deaths occurred in the ceftriaxone group, not only within 14 days after admission but also during the whole follow-up period to discharge from the TFC. However, the difference in total deaths during follow-up was not statistically significant (p = 0.62) and no p-value was reported for the former. The 13 deaths that occurred during the first 14 days were because of septic shock (n = 5), lower respiratory tract infections (n = 3), fluid overload (n = 4) and severe dehydration (n = 1).

Weight gain

Table 37 presents the primary outcomes on weight gain from the Dubray and colleagues59 study, which were success rate and mean overall weight gain, as well as a secondary outcome of weight gain at exit from TFC. The reported success rate is defined as a weight gain ≥ 10 g/kg/day by day 14 or discharge before 14 days of weight gain because the TFC exit criteria were met (maintained W/H ≥ 85% for 7 consecutive days). Mean overall weight gain was calculated 14 days after the first weight gain. The groups showed similar results and no statistically significant differences were found between groups for any of the outcomes.

Length of stay and reasons for exit from the therapeutic feeding centre

As shown in Table 38, the authors reported a slightly shorter length of stay for the ceftriaxone group, but the difference from the amoxicillin control group was not statistically significant. No statistically significant differences were found on the reasons for exit either.

Infection-related deaths and adverse events

Dubray and colleagues59 reported the number of infection-related deaths per type of infection and adverse effects attributed to antibiotics (Table 39). A statistically significant lower rate of adverse events was found in the ceftriaxone group (p = 0.05).

Summary

• One RCT59 that compared ceftriaxone (i.m.) with oral amoxicillin met the inclusion criteria of the review for this question. The RCT’s methodological quality was summarised as moderate, mainly owing to the fact that blinding of the outcome assessors or the participants was not carried out.

• Mortality was a secondary outcome of the RCT. Dubray and colleagues59 did not find a statistically significant difference in mortality between the ceftriaxone and amoxicillin groups. Similarly, no statistically significant differences in the number of recovered patients, weight gain, length of stay or reasons for exit from the TFC were found either.

• A statistically significant lower rate of adverse events was found in participants receiving ceftriaxone (p = 0.05) than in those receiving amoxicillin.

• No data on resolution of existing infections, development of new infections, relapse or development of antibiotic resistance outcomes were reported.

• The criteria used to define SAM were broadly in line with current WHO criteria, hence, results are likely to be generalisable to the SAM populations identified by WHO criteria. However, the generalisability to settings where HIV prevalence is high and where children may be receiving long-term cotrimoxazole prophylaxis is uncertain.

• More than 25% of children in each group received a second antimicrobial treatment (ceftriaxone, chloramphenicol, cotrimoxazole, amoxicillin or metronidazole, in accordance with TFC treatment protocols), which may have reduced the evidence of difference between groups.

• The study site was chosen because the working conditions were satisfactory, the centre adhered to international standards of nutritional rehabilitation programmes and the political situation was stable. Centres with poorer operational conditions might not be able to reach the same level of care, which might adversely affect outcomes.

Summary of quality assessment

Trehan and colleagues’ retrospective analysis of two cohorts60 was rated moderate in terms of its overall methodological quality (Table 41). The study was judged to be at a low risk of selection bias (rated strong for selection bias), but because this was a cohort with control study a moderate rating was applied for study design. Although there were some important differences between the cohorts prior to the intervention, the study authors indicated that these were taken into account in the analysis, which enabled the confounders section of the quality assessment to be judged strong. Although study participants were not aware of the research question, the outcome assessors knew what treatment participants had received, which led to a moderate rating for the blinding section. The data collection methods were rated weak because tools were not reported to be either valid or reliable. The final section contributing to the global rating, withdrawals and dropouts, was rated strong because 80–100% of participants completed the study, so the risk of bias owing to missing data was considered to be low. The intervention integrity is difficult to determine because the consistency of the intervention did not appear to have been measured, and it was not possible to tell whether or not any unintended intervention could have occurred in either cohort. There was also some uncertainty regarding the analysis of the data. The study was powered to detect a difference of at least 5% in the recovery rate.

Mortality

Mortality was one of the secondary outcomes of the Trehan and colleagues study. 60 The total number of deaths was reported at 4 weeks and at 12 weeks for the overall number of participants in each cohort, but also reported separately for those with and without oedema at baseline (Table 42). The rates of death at both time points were described as similar for each group.

Recovery

Recovery was defined as a W/H z-score ≥ –2 and no peripheral oedema (Table 43). Those who remained alive but did not meet the criteria for recovery were classed as remaining malnourished, and those who missed two follow-up visits were categorised as defaulters. At the 4-week follow-up, a greater proportion of children in the RUTF-only cohort had recovered in comparison with the cohort receiving amoxicillin and RUTF (70.8% vs 39.8%; no p-value reported). A statistically significant difference (p < 0.001) in favour of the RUTF-only cohort was reported for the subgroups of children with and without oedema at baseline. In the subgroup of children who recovered after 4 weeks, the W/H z-score was significantly higher in the RUTF cohort than in the RUTF plus amoxicillin cohort (–0.37 vs –0.75; p < 0.0001).

At the 12-week follow-up, the overall proportion who had recovered in each cohort was described as similar (no p-value reported). Rates of defaulting were described as similar in the two cohorts at 4 and 12 weeks (no p-values reported). Therefore, the proportions of children classed as remaining malnourished were as expected, with a greater proportion remaining malnourished at the 4-week follow-up in the intervention cohort receiving amoxicillin, but more similar proportions from each cohort were malnourished by the 12-week follow-up (no p-values reported for the between group comparison at either time point).

Other outcomes

A regression analysis was conducted to compare recovery rates, while controlling for differences in baseline characteristics between the cohorts. The model based on outcomes at 4 weeks showed that age (older children) and W/H z-score (higher W/H z-score) at baseline were predictive of recovery (p < 0.001 for both), whereas receipt of amoxicillin was correlated with failure to recover at 4 weeks (OR 0.22; p < 0.001). However, the 12-week follow-up regression analysis demonstrated that none of the baseline factors considered were predictive of recovery. The W/A z-score, H/A z-score and presence of oedema were not correlated with recovery in either the 4- or 12-week analysis. Full results are available in Appendix 10.

Summary

• One cohort study60 of moderate methodological quality compared amoxicillin plus RUTF with RUTF only for the treatment of uncomplicated SAM in children.

• Mortality rates were < 5% and similar in both cohorts.

• The primary outcome of the study was recovery rate (W/H z-score ≥ –2 and no peripheral oedema), which appeared substantially greater at 4 weeks in the cohort of children who did not receive amoxicillin. However, by 12 weeks the proportion of children in each cohort who had recovered was described as similar.

• The provision of a 7-day course of amoxicillin did not improve recovery rates from uncomplicated SAM in children in Malawi in this cohort when compared with the outcomes of a cohort who did not receive amoxicillin.

Summary of quality assessment

As summarised in Table 45, the overall methodological quality for two of the trials62,63 was found to be moderate, while for the remaining two trials it was found to be weak. 64,65

All four trials were judged to be at moderate risk of selection bias because, although 80–100% of the selected individuals participated in each of the four trials, their selected participants were judged as only somewhat likely to be representative of the target population. Two of the trials62,64 stated that children were randomly allocated to groups; however, during quality assessment they were judged to be CCTs (in accordance with the instructions on the use of the quality assessment tool, see Appendix 4) because the method of randomisation was not described. Nevertheless, the quality assessment tool still led to the trials being rated strong in terms of study design. Ciliberto and colleagues’ study,63 was the only trial with important differences between groups at baseline (including differences in W/H, details in Appendix 11), but as 80–100% of the relevant confounders were controlled for in the analysis, all trials were rated strong with respect to confounders.

All trials showed weak methodological quality on blinding, as the outcome assessor was not blinded in three of the studies62,64,65 (Ciliberto and colleagues63 is unclear on this matter) nor were the participants blinded in any of them. The studies by Chapko and colleagues62 and Ciliberto and colleagues63 were found to be moderate regarding data collection methods, as their tools were valid, but their reliability was not reported. The Heikens and colleagues64 study was rated weak for data collection methods because information on the validity and reliability of the methods used was not reported. Khanum and colleagues65 used valid and reliable methods for the second follow-up after an additional 12 months, and hence, their study was rated as strong; however, the validity of the tools of the initial study could not be determined and their reliability was not reported, so this initial study was classified as weak. Three of the studies had 80–100% of their participants completing the study; hence, they were rated strong on withdrawals and dropouts, in spite of the fact that only Heikens and colleagues64 reported on both the numbers and reasons for missing data.

Studies vary widely in terms of the integrity of intervention. Chapko and colleagues62 reported that some children did not receive the assigned care; in particular, 11% of those assigned to ambulatory treatment received hospital rehabilitation at the insistence of their mothers, but it was not clear whether or not any of the children assigned to hospital care did not attend. Khanum and colleagues65 reported that 60–79% of their participants received their allocated intervention, and the other two trials63,64 reported 80–100%. Consistency was reported to have been measured by one trial65 and not measured by two trials;62,63 one trial was not clear on the matter. 64 Contamination or co-intervention was likely to have occurred in Chapko and colleagues62 trial, whereas the other three studies63–65 are not clear on this aspect.

The infant/child was the unit of allocation in three trials,62,64,65 whereas allocation was established per rehabilitation centre by Ciliberto and colleagues,63 whose trial had a stepped-wedge design. The unit of analysis in all four included trials was the infant/child. Overall, statistical methods were found to be appropriate for the design of two of the included studies,62,64 but it was unclear if they were appropriate for the other two studies. 63,65 Out of the four studies, only Ciliberto and colleagues63 conducted an ITT analysis.

Mortality

Although mortality was a primary outcome of the Chapko and colleagues62 study and the Ciliberto and colleagues63 study, Khanum and colleagues65 reported it as a secondary outcome. None of the studies reported statistically significant differences in mortality between the different settings (Table 46). Chapko and colleagues62 reported a higher proportion of deaths in children in hospital than in the ambulatory setting. Ciliberto and colleagues63 reported only a 2.5% (95% CI –0.8% to 6.8%) difference in mortality between the groups, whereas Khanum and colleagues65 reported that mortality was low and did not differ between the groups (no p-value reported). Heikens and colleagues64 did not specify mortality as an outcome, but reported deaths among data on children lost to follow-up, and consequently no p-value was reported.

The authors of the included studies63–65 accounted for the number of deaths that occurred in both the initial and the rehabilitation phases, apart from Chapko and colleagues,62 who reported deaths in the rehabilitation period only. This study had the highest proportion of deaths.

Weight gain

One study, that by Chapko and colleagues,62 did not include weight gain as an outcome. Khanum and colleagues65 reported the mean weight gain from admission to 80% W/H as a primary outcome and weight gain after an additional 12 months’ follow-up as a secondary outcome (Table 47). A statistically significant difference in the primary outcome was found (p < 0.001), with inpatient care resulting in a greater daily mean weight gain from admission to the point at which participants reached 80% W/H than either home care or day care. However, after an additional 12 months of follow-up for all participants who reached 80% W/H, no significant differences in weight gain were apparent. Heikens and colleagues64 stated either that the rates of weight gain were similar or that there was no difference between the groups at the different treatment stages, but it is not clear whether or not any formal statistical testing was conducted and no p-values were reported. The exception was the average final rate of weight gain before discharge of 6–7 g/kg/day. The authors stated that this was maintained over a longer period for the long-stay group, but presented no data. Ciliberto and colleagues63 reported a non-statistically significant difference in the rate of weight gain for children at home compared with hospital during the first 4 weeks of the study. However, Ciliberto and colleagues63 performed a multivariate regression analysis, which showed that the overall rate of weight gain was 1.4 (95% CI 1.1 to 1.7) times as great among the severely malnourished children in those subject to home-based therapy than in those who received standard therapy at the rehabilitation unit.

Anthropometry

Chapko and colleagues62 reported W/H data in line graphs separately for those who died and for those who survived. Within both groups, there was no significant difference between the ambulatory-based and hospital-based groups (no p-value reported). Heikens and colleagues64 reported measures of W/H, W/A and H/A at discharge, after 6 months’ home care (end of intervention) and then at 6-month intervals to 36 months post admission (groups altered in size at later time points; see Appendix 11). At discharge, the hospital (long-stay) group had a better W/H z-score than the home (short-stay) group and the difference between the groups was statistically significant [mean z-score ± standard error (SE): long-stay group –0.49 ± 0.11 vs –1.17 ± 0.16 in the short-stay group; p = 0.001]64 (Table 48). However, 6 and 12 months later, the difference between the groups was no longer statistically significant (p-values 0.105 and < 0.1, respectively), and the difference between the groups narrowed further at 18 months and at later time points (no p-values reported). Ciliberto and colleagues63 found a statistically significantly higher proportion of patients with W/H > –2 SD after 8 weeks of treatment in the group under home-based therapy than in the inpatient group.

Weight-for-age and H/A outcomes were reported only by Heikens and colleagues. 64 Statistically significantly higher z-scores were reported for the long-stay group up to 24 months (W/A) or 30 months (H/A), but not thereafter (see Table 48 and Appendix 11).

Only Ciliberto and colleagues63 reported MUAC gain, finding a statistically significantly higher rate of MUAC gain during the first 4 weeks in the group under home-based therapy compared with the inpatient group.

Completion of treatment

Khanum and colleagues65 reported a significantly longer period of time to achieve 80% W/H in the group treated at home than in the group receiving hospital or ambulatory care (Table 49). The hospital (long-stay) group in the Heikens and colleagues64 study was considered to have completed treatment and was discharged when 95–100% W/H was reached (a mean ± SE of 39.45 ± 2.35 days post admission), but these data were not presented for the group that received care at home.

Relapse

Ciliberto and colleagues63 presented the composite outcome of children who relapsed or died (Table 50). It is presumed (although not explicitly stated) that this outcome incorporates the deaths already reported in Table 46, indicating, therefore, that 12 children (10.6%) in the hospital group relapsed, in comparison with 33 (6.2%) in the home group. A multivariate regression analysis was conducted to control for a range of covariates, and this indicated a statistically significantly lower probability of relapse or death [0.5 times (95% CI 0.3 times to 0.7 times)] in the subgroup of SAM children who received home-based therapy with RUTF compared with those receiving standard care at hospital. Khanum and colleagues65 reported on those who were readmitted during the 12-month follow-up. Children were readmitted if they relapsed (became oedematous or were < 60% W/H) or because of medical emergencies. Overall, there were eight readmissions (1.8% of the 437 children followed up), of which 0.6% occurred because of relapse. Data were not presented separately for relapse in each group, but Khanum and colleagues65 stated that relapse did not differ among the groups.

Additional outcomes

Other outcomes such as height gain, oedema loss and prevalence of fever, cough or diarrhoea were reported by some studies, but details have not been presented here. Full details are available in the data extraction forms in Appendix 11.

Summary

• One moderate-quality CCT was found comparing ambulatory care with hospital care. 62 Two other included CCTs involved home- and hospital-based therapy (one of them was graded moderate,63 whereas the other CCT’s methodological quality was considered weak64), and another methodologically weak CCT65 compared the three settings.

• Only one trial63 undertook an ITT analysis. There is the possibility, therefore, that the results of the remaining trials62,64,65 are at a higher risk of bias and, consequently, the intervention effect may not have been accurately captured.

• None of the included studies reported a significant difference in mortality between groups.

• Conflicting results were obtained for weight gain. No significant differences in weight gain during the first 4 weeks,63 at 12 months of follow-up65 or in the different stages up to 6 months after discharge64 were found between settings. However, a separate multivariate regression analysis in one trial found that overall rate of weight gain was greater among children in the home-based group than in those receiving standard therapy at the rehabilitation unit. 63 In contrast, two studies of weaker quality64,65 reported that inpatient care presented a statistically significantly higher mean weight gain to 80% W/H than home or ambulatory care,65 and the final average rate of weight gain was maintained over a longer period in the inpatient group than in the home-care group. 64

• There was no significant difference during a 6-month follow-up period in W/H between the ambulatory and hospital-based groups in one study. 62 However, two studies63,64 showed conflicting results for the comparison of hospital and home care. According to Heikens and colleagues,64 the inpatient group showed statistically significant improvement in W/H at discharge compared with the home-based group (supported by CHAs). In contrast, Ciliberto and colleagues’63 home-based group (visiting the rehabilitation centre fortnightly) included a statistically significantly higher proportion of patients with W/H > –2 SD after 8 weeks of treatment than in the inpatient group.

• Statistically significantly higher W/A and H/A z-scores were found after hospital-based treatment than after home care with support of CHAs. 64 In contrast, another trial reported a statistically significantly higher rate of MUAC gain during the first 4 weeks in the group under home-based therapy than in the inpatient group. 63

• Most studies defined SAM with criteria similar to those currently used by the WHO or analysed a subgroup that met them. 62,63,65 It is not clear, however, whether or not the participants in Heikens and colleagues’ study64 would meet current WHO criteria.

• Studies varied in the care provided, even if the same setting is considered. For instance, studies on home rehabilitation63–65 involved different diets, time and frequency of contact with nutritional rehabilitation centres/staff. Additionally, Chapko and colleagues62 point out that nutritional rehabilitation differed between ambulatory centres, and between the hospital and the ambulatory centres. Ciliberto and colleagues63 provide no indication regarding similarities or differences between centres.

Summary of quality assessment

The trials were assessed against a number of criteria to obtain an overview of their methodological quality. The global rating for methodological quality varied: two trials68,69,79 were rated strong overall, two trials74–76 were rated moderate and six trials were rated weak70–73,77,78 (Table 53).

The assessment of selection bias required a judgement about how likely it was that participants selected to take part in the study were representative of the target population and information about the percentage of selected individuals who did participate. In general, this information was not well reported. Consequently, only two studies74,75,79 were rated ‘strong’ (at low risk of selection bias). Of the remaining studies, four had a moderate rating68,69,73,77,78 and four had a weak rating70–72,76 (the latter judged to be at a high risk of selection bias).

The study design of all 10 trials was strong, with two being RCTs68,69,79 and the remaining eight being CCTs70–78 (in two of these,72,74,75 there was a suggestion of randomisation but no information was provided about the method, hence they were judged to be CCTs). Both of the RCTs68,69,79 and four of the CCTs71,73,76,77 were judged to have trial arms that were balanced with respect to baseline characteristics and confounders, leading to a strong rating. Reporting in the remaining four CCTs70,72,74,75,78 was either insufficient or unclear, so it was not possible to be certain whether or not the trial arms were balanced, which led to a weak rating. Six trials68,69,72,74–76,78,79 were described as double-blind; of these, five used a placebo and were judged strong with respect to blinding. 68,69,72,74,75,78,79 One trial76 was judged moderate because it was not clear whether or not the outcome assessor was blinded to the intervention status of the participants. Four trials,70,71,73,77 that did not use a placebo were all judged weak with respect to blinding.

When judging the methodological quality of data collection methods, the judgement could differ depending on the outcome measure. Therefore, the data collection method judgements reported here are for the primary outcomes of this systematic review (see Appendix 12). In five trials,71–73,77,78 the data collection tool was not described and, therefore, could not be judged as valid or reliable. The remaining trials all used valid data collection tools, but only two trials68,69,76 provided information indicating that the tools were reliable, which allowed data collection to be judged strong. The other three trials,70,74,75,79 were rated as moderate because no information about the reliability of the tools was reported. Most of the studies were rated as methodologically strong for the item on reporting of withdrawals and dropouts, even though six studies70–73,76,78 did not report the number and reasons for withdrawals and dropouts. The strong rating could be applied because the proportion of participants completing these studies lay between 80% and 100%. Only two studies did not gain a strong rating: one70 was judged moderate and one72 was judged weak because < 60% of participants completed the study.

The final two elements of the quality assessment tool, ‘intervention integrity’ and ‘analysis appropriate to question’, did not contribute to the global rating, but nevertheless provided important information about each study. In all studies, 80–100% of participants received their allocated intervention, in six trials the consistency of the intervention was measured,71,73,76–79 and in eight trials70–73,76–79 it was judged unlikely that any unintended intervention had been implemented. All studies allocated individual infants/children to trial arms and in only one study72 was there insufficient detail to determine whether or not appropriate statistical methods had been used. Three studies71,76,79 performed an ITT analysis.

Mortality

Mortality was reported by only two of the studies68,69,74,75 investigating zinc as a supplement (Table 54). Doherty and colleagues68,69 conducted a planned interim analysis of the first 100 participants. Data from the two groups receiving 6 mg/kg zinc were combined and, when compared with the group receiving 1.5 mg/kg zinc, the risk of death in the 90-day study period was significantly greater for those receiving 6 mg/kg (Yates’-corrected chi-squared value of risk of death 4.52, 95% CI for relative risk of 1.09 to 18.8; p = 0.03). This led to the suspension of enrolment to the trial, by which point 141 participants had been recruited. Of the 19 deaths that occurred overall (all three groups combined), 13 occurred during the inpatient phase and 11 of these occurred in one of the two 6 mg/kg zinc groups. The six deaths in the outpatient phase all occurred in children who had received 6 mg/kg zinc as inpatients (intervention group two who subsequently received placebo in the outpatient phase) or were still receiving 6 mg/kg zinc (intervention group 3). The clinician’s impression was that sepsis was the cause of death in most cases. Doherty and colleagues68,69 conducted an analysis of a range of predictive/prognostic factors, but found that none of these factors in conjunction with the higher dose of zinc was predictive for death.

Makonnen and colleagues74,75 also recorded the majority of deaths during the initial period of hospitalisation. However, in this trial the authors state that there were significantly more deaths in the control group, who did not receive a zinc supplement, than in the group that did receive a zinc supplement [17.3% mortality in the control vs 4.7% in the zinc group; no p-value given, but a 95% CI of 5.5% to 19.5% was reported (although not clear in the paper, it appears that this is likely to be the 95% CI for the difference between the groups)]. In each group, some participants had to be readmitted after discharge. In the zinc group, two participants were readmitted, one 5 days after discharge, who was subsequently discharged, and a second identified at the 30-day follow-up who subsequently died. In the control group, four participants were readmitted, three after initial discharge, of whom one subsequently died; the fourth was identified at the 30-day follow-up and also subsequently died.

Weight gain

Seven studies reported weight gain as an outcome, although the reported measures varied: overall weight gain, daily or weekly weight gain, grams of weight gained per kg body weight per day and proportion meeting a threshold value of weight gain (Table 55). All the studies except that by Gatheru and colleagues70 reported weight gain relative to initial weight or reported the proportion of participants meeting a threshold that was a measure of relative weight gain. These measures help remove differences due to starting differences in body weight. Three studies,70,73,77 reported at least one statistically significant difference in a weight gain outcome between the groups in favour of zinc supplementation, but four studies71,72,78,79 found no evidence for a statistically significant difference between groups. A meta-analysis was not carried out because it was considered to be inappropriate because of heterogeneity in the dose(s) of zinc provided, differences in the reported outcome measures [units and time point(s) of measurement] and other limitations of the data (missing measure of variance).

Gatheru and colleagues70 reported a significantly greater total weight gain in the zinc-supplemented group than in the control group (mean ± SD, 531 ± 277 g vs 338 ± 235 g; p < 0.05). However as noted above, the measures used in this study do not take into account starting differences in body weight. Approximately one-quarter of each group did not complete the study, but the reasons for this are not provided and it is not clear whether or not this had any impact on the outcome. Mean daily weight gain was greater in the zinc-supplemented group (67 g/day) than in the control group (47.3 g/day), but no p-value for a statistical comparison of these values was reported.

Khanum and colleagues73 found that during the first 2 weeks of rehabilitation (which was before zinc supplementation began), the rate of weight gain was not significantly different between the groups (see Appendix 12). However, at the start of the third week the intervention group started to receive a zinc supplement and Khanum and colleagues73 found that by the end of that week the group receiving the zinc supplement had gained significantly more weight than the non-supplemented group (mean ± SE: zinc group 580 ± 67.6 g/week, control group 342 ± 86.5 g/week; p < 0.05). This statistically significant effect was maintained in the following week, but by the fifth week of the study (after 3 weeks of zinc supplementation), the difference in weekly weight gain was no longer statistically significant. Khanum and colleagues73 also report that the percentage of participants in the zinc-supplemented group who achieved a mean daily weight gain of > 10 g/kg was statistically significantly greater than in the control group (66% vs 33%; p < 0.02). It is not clear for what time period the mean daily weight gain was calculated.

Simmer and colleagues77 also reported that the percentage of participants in the zinc-supplemented group who achieved a mean daily weight gain of > 10 g/kg was statistically significantly greater than in the control group (42% vs 9%; p < 0.001). However, in this study, although the zinc group gained more weight each week than the control group, statistically significant differences between the groups for mean daily weight gain and mean daily weight gain per kg body weight could not be demonstrated in either week 1 (see Appendix 12) or week 2 (see Table 55).

All four of the studies71,72,78,79 that did not find evidence for a statistically significant difference between groups reported on the rate of weight gain in terms of g/kg/day (the benefit of a relative measure such as g/kg/day is that any effects due to starting differences in body weight are removed). Golden and colleagues71 reported mean weight gain during the first 6 weeks of recovery. Although children in the moderate- and high-zinc groups gained weight more rapidly, the difference between the groups was not significant. Hemalatha and colleagues72 reported on this outcome separately for weeks 1, 2 and 3 (see Appendix 12) where gains appeared similar between groups, and for week 4 (see Table 55) when the difference in outcome was described as not statistically significant (mean ± SE: 22.6 ± 5.100 g/kg/day in the zinc group vs 24.5 ± 5.035 g/kg/day in the control group; no p-value reported). Bhutta and colleagues79 reported g/kg/day weight gained separately for the 14 days of inpatient and for the following 14 days of home-based supplementation. In both cases, although the zinc-supplemented group gained a little more weight than the control group and the differences were not found to be statistically significant (see Table 55; no p-value reported). Bhutta and colleagues also reported the total weight of children at baseline, on day 7 (see Appendix 12) and on day 14 of inpatient therapy, but again there was no significant difference between the groups (mean weight on day 14 in the supplemented group 6.67 ± 1.43 kg vs 7.13 ± 1.42 kg in the placebo group; p = 0.27). Finally, Vasudevan and colleagues78 reported a rate of weight gain in terms of g/kg/day, which was much lower than that of the other studies (zinc-supplemented group 1.4 g/kg/day vs 0.98 g/kg/day in the control group; p > 0.1). This lower value may be because the authors appear to have based their calculation on the initial weight and a single further weight measurement taken after 3 months.

Anthropometry

Five studies reported anthropometry outcomes (Table 56). 68,69,73–76,79 Two of these studies also reported weight gain as a separate measure,73,79 but anthropometry outcomes were the only measures capturing weight gain for the other three studies. 68,69,74–76 One study73 reported a statistically significant difference in anthropometry outcomes between the groups in favour of zinc supplementation, two studies reported mixed results74–76 and two studies found no evidence for a statistically significant difference between groups. 68,69,79 It was considered inappropriate to carry out a meta-analysis of these outcomes because of heterogeneity in the dose(s) of zinc provided and differences in the reported outcome measures.

Khanum and colleagues73 reported statistically significant differences in favour of zinc supplementation in measures of W/H, W/A and the percentage of patients reaching or exceeding 90% W/H by discharge. There were no significant differences in W/H and W/A at admission (see Appendix 12), but a significant difference in favour of the zinc group was present in W/H by the beginning of the first week (eighth day) and in W/A by the beginning of the second week of nutritional therapy (15th day). As zinc supplementation only began on day 15, it is not clear what led to the differences emerging at this stage. The differences were then maintained for each of the following weeks during zinc supplementation (see Appendix 12) until discharge on day 36 (at discharge W/H in the zinc group 95 ± 1.2, control 86 ± 1.2, p < 0.001; W/A in the zinc group 68.1 ± 1.58, control 59.7 ± 1.77, p < 0.001). Over 75% of participants were discharged with a W/H of ≥ 90% of that expected in the zinc-supplemented group, whereas < 25% of the control group reached W/H of ≥ 90% of that expected at discharge.

Makonnen and colleagues74,75 found that at discharge from inpatient care (after a mean length of stay of approximately 11 days), there were no significant differences in anthropometry between the groups. However, the zinc group continued to receive supplements until 90 days after discharge, and at the 90-day follow-up the proportion of children with W/A < 60% was described as significantly lower in the zinc group than that of the control group (3.6% vs 13.8%, 95% CI for difference –17.2% to –3.1%; no p-value reported), and the proportion with W/A > 80% and no oedema was greater (58.7% vs 28.4%; no 95% CI for difference or p-value reported). The proportion of zinc-supplemented participants whose MUAC remained below the fifth percentile was also lower than those children in the control group (54.1% vs 77.9%, 95% CI for difference –35.2% to –11.5%; no p-value reported).

Schlesinger and colleagues76 reported outcomes after 105 days of supplementation, but this was the only study in which the participants were all < 1 year of age and so received liquid formula only. No significant difference between the groups was apparent when z-scores for H/A, W/A and W/H were analysed (see Table 56 and Appendix 12). However, there was a statistically significant difference in the proportion of infants in the zinc-supplemented group whose percentile H/A score increased after 30 and 45 days of nutritional rehabilitation, indicating that the zinc group began to grow earlier than the control group [58% (at 30 days) and 79% (at 45 days) of the 15 mg/l zinc group had an increase in their H/A percentile score in relation to their admission score in comparison with only 20% (at 30 days) and 45% (at 45 days) in the 3.2 mg/l zinc group; p < 0.002 and p < 0.03, respectively]. When these data were analysed by sex, the authors found that the effect held for males, but not for females (see Appendix 12). This difference was no longer significant after 60 days of nutritional rehabilitation (see Table 56).

Doherty and colleagues68,69 reported on the changes in W/A, W/H and H/A z-scores and MUAC (see Table 56), as well as knemometry and skinfold thickness (see Appendix 12). There were three groups in this study and two comparisons were made, the first between the 1.5 mg/kg and the 6 mg/kg zinc dose for 15 days and the second between the 6 mg/kg zinc dose for 15 days or for 30 days. The results reported after 90 days of follow-up indicated that no significant differences were reported for either comparison for any of the anthropometric measures reported. Doherty and colleagues68,69 did find that, overall, good catch-up growth was achieved over 90 days, with the average intragroup W/H z-score improved from 1.54 to 1.67 units, and the H/A z-score improved from 0.44 to 0.49 units.

Finally, Bhutta and colleagues79 reported on just the anthropometric measure of MUAC, finding no significant differences in this measure after 14 days of inpatient therapy (mean MUAC: zinc group 12.0 ± 1.4 cm vs 12.4 ± 1.8 cm in the placebo group; p = 0.66), and no significant differences emerged after a further 14 days of home-based supplementation (see Table 56).

Comorbidities

The effect of zinc supplementation on comorbidities was an outcome reported by five studies. 70,72,74–76,79 In three studies,70,72,79 at least some of these comorbidities had been present at baseline and the study authors report on the effect of the intervention in resolving these. In the study76 in which comorbidities were recorded daily for 105 days and the study74,75 reporting outcomes at 90-day follow-up, it is likely that new incidences of comorbidities are captured.

Three studies70,72,74,75 reported oedema as an outcome (Table 57). Gatheru and colleagues70 reported that the duration of oedema ranged between 2 and 18 days for both groups. However, a greater proportion of participants in the zinc group had lost their oedema by day 7 (77% vs 55%), and the mean number of days taken to lose oedema was statistically significantly lower in the zinc group (mean ± SD: zinc group 6.3 ± 4.6 days vs control group 8.1 ± 4.4 days; p < 0.05). In contrast, Hemalatha and colleagues72 found no statistically significant difference in the mean number of days taken to lose oedema (mean ± SE: zinc group 9.0 ± 2.0 days vs control group 15.7 ± 2.7 days). In the final study to report oedema, Makonnen and colleagues74,75 found a trend for the zinc group to recover more quickly during the first 3 weeks of hospitalisation, but the difference between the groups was not statistically significant (see Appendix 12) and by the 90-day follow-up no patient in either group had any oedema.