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Enteral zinc supplementation for prevention of morbidity and mortality in preterm neonates

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Versión publicada: 27 septiembre 2017 Historial de versiones

https://doi.org/10.1002/14651858.CD012797

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Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

Primary objectives are to assess the effectiveness and safety of enteral zinc supplementation versus no intervention or placebo on morbidity, growth, and neurodevelopmental development among preterm infants.

Secondary objectives include determining:

  • effects of enteral zinc supplementation on morbidities typically seen in preterm infants: bronchopulmonary dysplasia, retinopathy of prematurity, bacterial sepsis, necrotising enterocolitis, and intraventricular haemorrhage;

  • which infants would profit the most from enteral zinc supplementation (within predefined subgroups: gestational age, birth weight, types of enteral feeds);

  • the optimal dose of zinc supplementation: lower dose versus higher dose; or

  • the optimal duration of zinc supplementation: short‐term versus long‐term.

Background

Zinc is a trace element that acts as a co‐factor in more than 300 metalloenzymes, through which it is involved in growth, cell differentiation, gene transcription, major pathways of metabolism, and hormone and immune function. Therefore, zinc is indispensable for normal growth, tissue maintenance, and wound healing (Livingstone 2015). Zinc is absorbed in the upper gastrointestinal (GI) tract into enterocytes and is entered into a small plasma pool. The human organism has no dedicated zinc store. Rather, in states of excessive or decreased zinc intake, homeostasis is regulated through GI absorption, excretion via faeces or urine, and retention or release by selected tissues (King 2000).

Description of the condition

Overt zinc deficiency in children leads to stunted growth, immunosuppression, and a phenotypical skin disorder with diarrhoea (similar to the autosomal recessive acrodermatitis enteropathica), which was first described in the 1960s (Hambidge 2000). In low‐income and middle‐income countries, where the prevalence of zinc deficiency is highest, zinc supplementation in children has been shown to be an effective intervention for improvement of growth and prevention of infectious disease (Bhutta 1999; Brown 1998; Wessells 2012). More subtle zinc deficiency is difficult to diagnose owing to lack of reliable laboratory markers and less specific signs and symptoms (Hambidge 2000; King 2000).

Preterm infants start out with a smaller zinc pool than term infants, because 60% of zinc accretion takes place during the last trimester of pregnancy through transplacental transfer (Giles 2007). Accordingly, plasma zinc levels in cord blood are proportionately lower with younger gestational age and lower birth weight (Gomez 2015). Breast milk usually is well equipped with all micronutrients required for optimal growth and development of the term baby but may not provide enough zinc to match foetal accretion rates and very rapid postnatal growth rates. This leaves preterm and low birth weight babies at risk for symptomatic zinc deficiency. Symptoms of zinc deficiency include failure to thrive despite sufficient caloric intake, dermatitis, and increased susceptibility to infection (Obladen 1998). However, subclinical forms are likely to be more common and often go unrecognised. Some studies estimate the prevalence of subclinical zinc deficiency in preterm infants near term to be as high as 25% to over 50% (Itabashi 2003; Obladen 1998). Diagnosing relevant, yet asymptomatic, zinc deficiency is difficult because of the natural variation in zinc levels noted in preterm infants and the low sensitivity of plasma zinc levels for dietary deficiency (Altigani 1989; King 1990). Furthermore, no data indicate at what plasma level of zinc and/or in the presence of which co‐factors signs of zinc deficiency become clinically manifest in individual patients.

Description of the intervention

Both parenteral and enteral nutrition for preterm infants contain zinc that was added to prevent zinc deficiency. Recommendations for zinc intake in stable growing preterm infants range from 1 to 2.5 mg/kg/d up to 3 mg/kg/d for extremely low birth weight infants (Agostoni 2010; Domellof 2014; Kleinman 2014). These recommendations are in line with those provided by various retention studies and generally are met by current preterm formula and breast milk supplements (Finch 2015; Griffin 2013). However, in trials studying prevention of various diseases in different paediatric populations including preterm infants, zinc intake is often well above recommended nutrient intake (Bhutta 1999; Friel 1993; Mishra 2015; Terrin 2013).

How the intervention might work

High growth rates and rapidly developing organs render preterm infants crucially dependent on adequate intake of macronutrients and micronutrients, especially after they have missed out on an important time of transplacental nutrient transfer during the last trimester of pregnancy. Zinc is involved in a large variety of cellular functions, which is why even mild subclinical zinc deficiency could impair global as well as organ‐specific development of the preterm infant, notably of the brain and GI tract (Berni Canani 2010; Levenson 2011). Additionally, preterm infants are less efficient in absorbing and retaining zinc from the GI tract (King 2000; Voyer 1982). Therefore, they may profit from higher intake than mature infants and children for the purpose of improving growth and reducing the risk of morbidities typical for preterm infants, such as sepsis, necrotising enterocolitis, chronic lung disease, abnormal neurodevelopment, and retinopathy of prematurity. Specifically, zinc supplementation could improve immune function and the integrity of skin and mucosal barriers, notably in the GI tract, thereby improving feed tolerance, while reducing the incidence of infection and necrotising enterocolitis (Berni Canani 2010; Prasad 2008). Improved growth and cell repair could reduce the severity of chronic lung disease. Zinc is also a pivotal trace element in developmental neurogenesis, and supplementation could positively affect neuronal differentiation and development during the vulnerable period of prematurity (Levenson 2011). Zinc, the most abundant trace element in the retina, could play a role in normal eye development and function and may provide important antioxidant capacity, even though its role in prevention of retinopathy of prematurity has not been studied so far (Falchuk 1998; Grahn 2001). All of the benefits discussed above show the positive potential of zinc as a single trace element intervention for important clinical outcomes in preterm infants. From the existing literature, it remains unclear whether presumed benefits could be achieved with zinc supplementation over a defined period of a few weeks, or whether positive effects could be increased proportionately with increasing length of the intervention over multiple weeks or months.

Even though zinc supplements are considered relatively safe, enteral administration has the potential to negatively influence copper and iron absorption in the GI tract (Fosmire 1990; Livingstone 2015;Obladen 1998; Sugiura 2005). Therefore, zinc supplementation over and above the recommended daily intake requires careful monitoring and evaluation for patients who are dependent on balanced micronutrient intake.

Why it is important to do this review

Several non‐Cochrane and Cochrane systematic reviews have addressed zinc supplementation in the paediatric population beyond the neonatal age, with some showing beneficial effects on the respiratory tract and on diarrhoeal illness, but others reporting only marginal benefit (Aggarwal 2007; Bhutta 1999; Patel 2011; Roth 2010; Yakoob 2011). A few systematic reviews have reported improved growth following zinc supplementation, but another systematic review did not find convincing evidence (Brown 1998; Brown 2002; Imdad 2011;Ramakrishnan 2009). None of these reviews addresses neonates or preterm infants. A single review of three randomised trials (RCTs) examined zinc supplementation in breast‐fed low birth weight infants from low‐income and middle‐income countries and found no beneficial effect on mortality, infectious disease, or growth (Gulani 2011). However, no systematic review (Cochrane or non‐Cochrane) to date has addressed effects of zinc supplementation in preterm low birth weight or very low birth weight infants in the setting of their typically long stay in the neonatal intensive care unit and with regards to growth, mortality, morbidity specific for this population (such as bronchopulmonary dysplasia, intraventricular haemorrhage, necrotising enterocolitis), and developmental outcome. In reviews involving children beyond neonatal age, effects of zinc supplementation are most pronounced in those with low nutritional status before the intervention is received (Bhutta 1999; Gulani 2011; Yakoob 2011). Given these findings, it is reasonable to hypothesise that preterm babies, who are born with low zinc stores and with diminished capacity for zinc absorption and retention, could benefit from zinc supplements as an easily implemented intervention for growth, immune function, and decreased morbidity (Krebs 2014; Voyer 1982).

Objectives

Primary objectives are to assess the effectiveness and safety of enteral zinc supplementation versus no intervention or placebo on morbidity, growth, and neurodevelopmental development among preterm infants.

Secondary objectives include determining:

  • effects of enteral zinc supplementation on morbidities typically seen in preterm infants: bronchopulmonary dysplasia, retinopathy of prematurity, bacterial sepsis, necrotising enterocolitis, and intraventricular haemorrhage;

  • which infants would profit the most from enteral zinc supplementation (within predefined subgroups: gestational age, birth weight, types of enteral feeds);

  • the optimal dose of zinc supplementation: lower dose versus higher dose; or

  • the optimal duration of zinc supplementation: short‐term versus long‐term.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised (individual and cluster‐randomised) and quasi‐randomised controlled trials of zinc supplementation versus placebo or no intervention in preterm and low birth weight babies. We will exclude observational and cross‐over trials.

Types of participants

We will include studies that enrolled infants born preterm (gestational age < 37 weeks) and at low birth weight (birth weight < 2500 grams) and admitted to the neonatal intensive care unit or the special care unit or a comparable setting after birth. We will exclude infants who underwent GI surgery during their initial hospital stay, or had a GI malformation or another condition accompanied by abnormal losses of GI juices, which contain high levels of zinc (including, but not limited to, stomas, fistulas, and malabsorptive diarrhoea). If studies include participants with and without such presumed high GI zinc losses, we will contact study authors to request data on the former and to exclude these participants from the analysis. If this information is not available, we will exclude the respective study as a whole.

Types of interventions

Zinc supplementation in any formulation, regimen, or dose administered via the enteral route, in addition to a standard nutrition regimen (partial or full enteral feeds, breast milk, or formula) versus placebo or no intervention, starting at any time from birth to hospital discharge. We will include trials in which participants receive additional macronutrient and micronutrient supplementation and/or multi‐component milk fortification, as long as supplementation is the same in both intervention and non‐intervention/placebo groups, and as long as the actual intervention of enteral zinc supplementation or placebo is given in addition to macronutrients and micronutrients and milk fortification.

Types of outcome measures

We will include studies even if they do not report all outcomes. If a study does not report all outcomes, we will seek further information from trial authors.

Primary outcomes

  • All‐cause mortality

    • Before hospital discharge (latest time reported at or after 36 weeks' postmenstrual age)

    • Between hospital discharge and neurodevelopmental follow‐up at 18 to 24 months of age (post term)

  • Neurodevelopmental disability at 18 to 24 months of age (post term), defined as a neurological abnormality including any of the following

    • Cerebral palsy on clinical examination

    • Developmental delay > 2 SD below the population mean on a standardised test of development (Vohr 2004)

    • Blindness (visual acuity < 6/60)

    • Deafness (any hearing impairment requiring amplification)

Secondary outcomes

  • Bronchopulmonary dysplasia (BPD, according to Eunice Kennedy Shriver National Institute of Child Health and Human Development (NICHD) criteria, defined as oxygen requirement > 21% at 28 days of life) (Jobe 2001)

  • Breathing room air (mild BPD)

  • Oxygen requirement < 22% to 29% (moderate BPD)

  • Oxygen requirement > 30% and/or positive pressure (severe BDP) at 36 weeks' postmenstrual age (for infants born at < 32 weeks' gestation) or at 56 days of life or discharge, whichever is later (for infants born at ≥ 32 weeks' gestation)

  • Retinopathy of prematurity (any stage and stage III or IV)

  • Bacterial sepsis (proven episodes by means of positive blood culture)

  • Necrotising enterocolitis (any stage)

  • Intraventricular haemorrhage (grade III or IV)

  • Change in standardised growth: between start and end of intervention, from discharge to time of neurodevelopmental follow‐up at 18 to 24 months of age (post term) (change in z‐score for weight, length, and head circumference, where z‐score is defined as deviation of an observed value for an individual from the median value of the reference population, divided by the standard deviation of the reference population) (WHO 1995)

Additional outcomes

  • Differences in blood zinc levels (in µg/dL or µmol/L) between any time before and during/at the end of the intervention (at the latest time reported before the end of the intervention)

  • Skin eruptions or dermatitis at any time before or during the intervention as a clinical sign of zinc deficiency

Indicators of potential adverse effects of zinc supplementation include the following.

  • Differences in blood iron status (blood iron in µg/dL or µmol/L or ferritin in µg/L) between any time before and during/at the end of the intervention (at the latest time reported before the end of the intervention).

  • Differences in copper status (blood copper levels in µg/dL or µmol/L, serum ceruloplasmin in µg/dL or µmol/L) between any time before and during/at the end of the intervention (at the latest time reported before the end of the intervention).

Search methods for identification of studies

Electronic searches

We will conduct a comprehensive search including the Cochrane Central Register of Controlled Trials (CENTRAL; current issue) in the Cochrane Library; MEDLINE via PubMed (1996 to current); Embase (1980 to current); and the Cumulative Index to Nursing and Allied Health Literature (CINAHL; 1982 to current), using the following search terms: (zinc OR micronutrient* OR trace element*), plus database‐specific limiters for RCTs and neonates (see Appendix 1 for full search strategies for each database). We will not apply language restrictions. We will search clinical trials registries for ongoing and recently completed trials (www.ClinicalTrials.gov; the World Health Organization International Trials Registry and Platform; www.whoint/ictrp/search/en/; the ISRCTN Registry; www.controlled‐trials.com).

Searching other resources

We will examine the references of included studies and previous reviews identified as potentially relevant. We will handsearch abstracts from annual meetings of the Pediatric Academic Societies, the European Society for Paediatric Research, and the Perinatal Society of Australia and New Zealand, from 1990 (or from the year when electronic conference proceedings became available) to current. We will consider trials reported as abstracts only if sufficient information is provided in the report or through contact with trial authors to fulfil the inclusion criteria, and if final trial data rather than an interim analysis are available.

Data collection and analysis

Selection of studies

We will use standard methods of Cochrane and the Cochrane Neonatal Review Group (Higgins 2017).

Two review authors will independently assess the eligibility of trials against inclusion and exclusion criteria. We will select studies as potentially relevant by screening title and abstract and, if relevance cannot be ascertained by the latter method, by retrieving the full text of articles for review. We will retrieve full texts of all potentially relevant articles and will assess their eligibility independently by filling out eligibility forms designed in accordance with the specified inclusion and exclusion criteria. We will resolve disagreements by discussion and will document studies excluded from the review in the 'Characteristics of excluded studies' table, along with reasons for exclusion.

Data extraction and management

Two review authors will independently extract data from full‐text articles using a specifically designed spreadsheet to manage the information. We will resolve discrepancies through discussion or, if required, via consultation with a third review arbiter. We will enter data into Review Manager 5 software and will check data for accuracy (RevMan 2014). When information regarding any of the above is missing or unclear, we will attempt to contact authors of the original reports to clarify and obtain additional details.

Assessment of risk of bias in included studies

At least two review authors will independently assess study quality and risk of bias using the following criteria, which are documented in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017).

Sequence generation (to assess selection bias)

For each included study, we will analyse the method used to generate the allocation sequence, to determine whether the method should produce comparable groups. We will assess the method as:

  • low risk (random component in the sequence generation process, e.g. random number table; coin tossing; throwing of dice);

  • high risk (non‐random component in the sequence generation process, e.g. date of birth; date of admission; hospital record number); or

  • unclear risk.

Allocation concealment (to assess selection bias)

For each included study, we will analyse the method used to conceal the allocation sequence, to determine whether intervention allocation could have been foreseen in advance of or during recruitment, or changed after assignment. We will assess the method as:

  • low risk (participants and investigators enroling participants could not foresee assignment of allocations, e.g. telephone allocation, use of opaque sealed envelopes);

  • high risk (participants or investigators enroling participants could possibly foresee assignment of allocations, e.g. unsealed envelopes); or

  • unclear risk.

Blinding of participants and personnel (to assess performance bias)

For each included study, we will analyse the method used to blind participants and their parents (as the study population consists of neonates, all participants would be blinded to the intervention, but not necessarily parents/caregivers) and personnel from knowledge of which intervention a participant received. We will assess the method as:

  • low risk (e.g. blinding of participants/parents and key study personnel);

  • high risk (e.g. no blinding or incomplete blinding of participants and key study personnel); or

  • unclear risk.

Blinding of outcome assessment (to assess detection bias)

For each included study, we will analyse the method used to blind outcome assessors from knowledge of which intervention a participant received. We will assess the method as:

  • low risk (e.g. blinding of outcome assessment ensured);

  • high risk (e.g. no blinding of outcome assessment); or

  • unclear risk.

Incomplete outcome data (to assess attrition bias)

For each included study, we will analyse completeness of data, including attrition and exclusions from the analysis. We will state whether attrition and exclusions were reported, numbers included in the analysis at each stage (compared with total numbers of randomised participants), reasons for attrition or exclusion when reported, and whether missing data were balanced across groups or were related to outcomes. We will compare published study results versus published protocols (or will contact study authors for study protocols in case the protocol was not published in advance). We will assess completeness of data as:

  • low risk (e.g. no missing outcome data, < 20% missing data);

  • high risk (e.g. reason for missing outcome data likely to be related to true outcome, > 20% missing data); or

  • unclear risk.

Selective reporting (to assess reporting bias)

For each included study, we will investigate the possibility of selective outcome reporting bias. For studies in which study protocols were published in advance, we will compare prespecified outcomes versus outcomes eventually reported in the published results. If the study protocol was not published in advance, we will contact study authors to gain access to the study protocol. We will assess the method as:

  • low risk (e.g. study protocol is available and all of the study's prespecified (primary and secondary) outcomes were reported in the prespecified way);

  • high risk (e.g. not all of the study's prespecified primary outcomes were reported); or

  • unclear risk.

Overall risk of bias

We will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017). We will assess the likely magnitude and direction of bias, and whether we consider it likely to impact our findings. We will explore the impact of the level of bias by performing sensitivity analyses ‐ see below. If necessary, we will request additional information and clarification from the original investigators.

Measures of treatment effect

We will follow standard methods of the Cochrane Neonatal Review Group for data synthesis, using Review Manager 5 software (RevMan 2014). We will report dichotomous data or categorical data using risk ratios (RRs), relative risk differences (RDs), and, for significant risk difference, number needed to treat for an additional beneficial outcome (NNTB) or for an additional harmful outcome (NNTH). We will obtain means and standard deviations (SDs) for continuous data and will perform analysis using mean differences (MDs) and standardised mean differences (SMDs) to combine trials that measure the same using different scales. For each measure of effect, we will provide the corresponding 95% confidence interval (CI).

Unit of analysis issues

We will include cluster‐randomised trials in the analyses along with individually randomised trials using an estimate of the intracluster correlation co‐efficient (ICC) derived from the trial (if possible). We will consider it reasonable to combine the results of individually randomised and cluster‐randomised trials if we note little heterogeneity between study designs, and if the interaction between effect of the intervention and choice of randomisation unit is considered unlikely.      

Dealing with missing data

We will contact authors of all published trials if we require clarification or additional information. In the case of missing data, we will describe the number of participants with missing data in the Results section and in the 'Characteristics of included studies' table. We will present results only for available participants and will explore in the Discussion section implications of the missing data.

Assessment of heterogeneity

We will assess heterogeneity of treatment effects between trials by using the following statistical models (Higgins 2017).

  • I2 statistic, a quantity that indicates the proportion of variation of point estimates that is due to variability across studies rather than to sampling error (i.e. to ensure that pooling of data is valid). We will grade the degree of heterogeneity as none (< 25%), low (25% to 49%), moderate (50% to 74%), or high (75% to 100%).

  • Chi2 test: a quantity that assesses whether observed variability in effect sizes between studies is greater than would be expected by chance.

When we find evidence of apparent or statistical heterogeneity, we will assess the source of the heterogeneity using sensitivity and subgroup analyses to look for evidence of bias or methodological differences between trials.

Assessment of reporting biases

We will explore publication bias by using funnel plots if we include at least 10 studies in the systematic review (Egger 1997; Higgins 2017).

Data synthesis

We will perform statistical analyses according to recommendations of the Cochrane Neonatal Review Group (http://neonatal.cochrane.org) using Review Manager 5 software (RevMan 2014). We will analyse all infants randomised on an intention‐to‐treat basis as well as treatment effects examined in the individual trials described above. We will use a fixed‐effect model to combine data, unless we find moderate heterogeneity, in which case we will use a random‐effects model. We will use the generic inverse variance method to synthesise risk estimates. When we judge meta‐analysis to be inappropriate (i.e. if heterogeneity is judged high, > 75%), we will synthesise and interpret individual trials separately.

Quality of evidence

We will use the GRADE approach, as outlined in the GRADE Handbook, to assess the quality of evidence for the following (clinically relevant) outcomes (Schünemann 2013).

  • All‐cause mortality.

    • Before hospital discharge (latest time reported at or after 36 weeks' postmenstrual age).

    • Between hospital discharge and neurodevelopmental follow‐up at 18 to 24 months of age (post term).

  • Neurodevelopmental disability at 18 to 24 months of age (post term), defined as a neurological abnormality including any of the following.

    • Cerebral palsy on clinical examination.

    • Developmental delay > 2 SDs below the population mean on a standardised test of development (Vohr 2004).

    • Blindness (visual acuity < 6/60).

    • Deafness (any hearing impairment requiring amplification).

  • Bronchopulmonary dysplasia (BPD, according to NICHD criteria, defined as oxygen requirement > 21% at 28 days of life and:

    • breathing room air (mild BPD);

    • oxygen requirement < 22% to 29% (moderate BPD); or

    • oxygen requirement > 30% and/or positive pressure (severe BDP) at 36 weeks' postmenstrual age (for infants born at < 32 weeks' gestation) or at 56 days of life or discharge, whichever is later (for infants born at ≥ 32 weeks' gestation) (Jobe 2001).

  • Retinopathy of prematurity (any stage and stage III or IV).

  • Bacterial sepsis (episodes proven by means of positive blood culture).

  • Necrotising enterocolitis (any stage).

  • Intraventricular haemorrhage (grade III or IV).

  • Change in standardised growth.

Two review authors will independently assess the quality of evidence for each of the outcomes above. We will consider evidence from RCTs as high quality but will downgrade the evidence one level for serious (or two levels for very serious) limitations on the basis of the following: design (risk of bias), consistency across studies, directness of evidence, precision of estimates, and presence of publication bias. We will use GRADEproGDT to create a ‘Summary of findings’ table to report the quality of the evidence (GRADEpro).

We will use the GRADE approach to assess the quality of a body of evidence as one of four grades.

  • High: We are very confident that the true effect lies close to that of the estimate of the effect.

  • Moderate: We are moderately confident in the effect estimate: The true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.

  • Low: Our confidence in the effect estimate is limited: The true effect may be substantially different from the estimate of the effect.

  • Very low: We have very little confidence in the effect estimate: The true effect is likely to be substantially different from the estimate of effect.

Subgroup analysis and investigation of heterogeneity

If sufficient data are available, we will undertake the following a priori subgroup analysis to explore potential sources of clinical heterogeneity.

  • Gestational age (< 28 weeks, 28 to 32 weeks, > 32 weeks).

  • Birth weight (≤ 1500 grams, > 1500 grams).

  • Type of enteral feeds (predominantly or exclusively human milk, predominantly or exclusively formula feeds).

  • Dose of zinc supplementation (≤ 3 mg/kg/d, > 3 mg/kg/d).

  • Duration of zinc supplementation (≤ 4 weeks, > 4 weeks).

  • Additional micronutrient supplementation (zinc preparation alone, zinc combined with other micronutrients or vitamins).

Sensitivity analysis

We will explore methodological heterogeneity by performing sensitivity analyses (if sufficient data are available). We will perform sensitivity analyses by excluding trials of lower quality when we judge them to be at high risk of bias, to assess effects of bias on the meta‐analysis. We will define low quality as lack of any of the following: allocation concealment, adequate randomisation, blinding of treatment, or < 20% follow‐up.