Types of studies

All randomised and quasirandomised controlled trials (including cluster and parallel trials, and trials in which the infant serves as his/her own control) comparing the topical application of oils with the topical application of other oils, emollients or placebo, or with no treatment will be considered.

Types of participants

We will include newborn term (≥ 37 weeks of gestation) infants receiving the application of topical oils or emollients:

1. for the prevention of dry skin within the first 28 days following birth; or

2. for the treatment of dry skin within the first 28 days following birth.

There is no upper gestational age limit for eligibility.

For the purposes of this review, dry skin will be diagnosed using a validated skin assessment scoring tool (Lane 1993; Lund 2001) or skin surface hydration measurement tool (e.g. a Corneometer®), or by clinical observation by a midwifery, neonatal or dermatology health professional.

We will include infants with normal skin and infants with a family history of atopic eczema. Normal infant skin variations, such as erythema neonatorum, erythema toxicum or milia, will not be considered as skin disorders, and will therefore be included. A family history of atopic eczema will be defined as "at least one of mother, father or sibling who has a medical diagnosis of atopic eczema/atopic dermatitis and who is treated with topical steroidal treatment". Infants diagnosed with an impairment of epidermal integrity, abnormal epidermis or dermis, such as collodion infant or congenital ichthyosis, will be excluded.

We will exclude newborn preterm (< 37 weeks of gestation at birth) infants, as this population has been included in another review (Seliem 2009).

Types of interventions

All of the stated interventions will be considered separately for both the prevention and treatment of dry skin.

Intervention

1. Application of topical oils, which may include any type of oil (such as olive oil, sunflower oil, coconut oil, grape seed oil, borage oil, evening primrose oil, other vegetable oil) compared with placebo or no topical applications

2. Application of topical emollients compared with placebo or no topical applications

Other Interventions

1. Intervention oil versus another topical oil

2. Intervention emollient versus another topical application (such as emollient, gel, cream, lotion or powder)

3. Intervention oil versus another topical application (such as emollient, gel, cream, lotion or powder)

It is expected that other products, such as soaps or bathing products, may be used on the infants in the trials. It is also expected that there will be variations in the dose, area, frequency and duration of application of the interventions. If there are substantial differences across trials, data will not be pooled but reported separately. Where combinations of topical applications are applied, data from a combination of treatments will not be pooled with data for single treatments.

Types of outcome measures

Where appropriate, data will be pooled or, if necessary (and appropriate), dichotomised. Outcomes will be analysed at baseline and at further time points up to 28 days (e.g. 7, 14, 28 days).

Electronic searches

We will identify randomised controlled trials from the Cochrane Central Register of Controlled Trials (CENTRAL, latest issue of The Cochrane Library). We will identify all other trials from MEDLINE (1966 to current), EMBASE (1980 to current), CINAHL (1982 to current), Dissertation Abstracts (1980 to current) and SIGLE (2000 to current). We will list the full search strategies for these databases in the review. We will identify ongoing clinical trials through searching www.clinicaltrials.gov.

We will not apply any language restrictions. We will use the following text words or medical subject heading terms: infant, neonate, newborn, baby, plant oils, oils, emollients, oleic acid, oleic, linoleic, skin barrier function, epidermal barrier function, skin scores, atopic march, dry skin, atopic eczema, atopic dermatitis.

Searching other resources

We will search for further studies in the reference lists of all identified articles. We will not apply language, start date or geographical restrictions. We will approach the clinical research departments of all major pharmaceutical and cosmetic companies to request access to their unpublished research (see Appendix 1). We will contact subject experts to identify ongoing, unpublished research. Abstracts presented at the annual meetings of the Society for Pediatric Research, the American Pediatric Society, and the European Society for Paediatric Research, and published in the journal Pediatric Research, will be handsearched. We will include trials presented in abstract form only if sufficient data are available from the abstract, or from contact with the author.

Selection of studies

Two review authors (AC, TL) will independently assess for inclusion all the potential studies we identify as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult a third review author (SV or MC).

Data extraction and management

We will design a form for the extraction of data. For eligible studies, at least two review authors (AC, TL) will extract data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult a third review author (SV/MC). We will enter data into Review Manager (RevMan 2011) and check them for accuracy.

We will attempt to contact authors of the original reports to provide further details when information regarding the above is unclear.

Assessment of risk of bias in included studies

Two review authors (AC, TL) will independently assess the risk of bias in each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreement by discussion or by involving a third review author (SV/MC).

(1)    Sequence generation (checking for possible selection bias)

For each included study we will describe the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.

We will assess the method as:

• adequate (any truly random process, e.g. random number table; computer random number generator);

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

• unclear.

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

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

We will assess the methods as:

• adequate (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);

• inadequate (open random allocation; unsealed or non‐opaque envelopes; alternation; date of birth);

• unclear.

(3)    Blinding (checking for possible performance bias)

We will describe for each included study the methods used, if any, to blind outcome assessors, participants and personnel from knowledge of which intervention a participant received. We will judge studies at low risk of bias if they were blinded, or if we judge that the lack of blinding could not have affected the results. We will assess the methods for blinding separately under the headings: participants, personnel and outcomes.

We will assess the methods as:

• adequate;

• inadequate;

• unclear.

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

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

We will assess the methods as:

• adequate (where fewer than 20% of the data are missing);

• inadequate (where more than 20% of the data are missing);

• unclear.

(5)    Selective reporting bias

We will describe for each included study how we investigated the possibility of selective outcome reporting bias and what we found.

We will assess the methods as:

• adequate (where it is clear that all of the study’s prespecified outcomes and all expected outcomes of interest to the review have been reported);

• inadequate (where not all of the study’s prespecified outcomes have been reported; one or more reported primary outcomes were not prespecified; outcomes of interest are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);

• unclear.

(6)    Other sources of bias

We will describe for each included study any important concerns we have about other possible sources of bias.

We will assess whether each study was free of other problems that could put it at risk of bias as:

• yes;

• no;

• unclear.

(7)    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 2011). With reference to (1) to (6) above, we will assess the likely magnitude and direction of the bias, and whether we consider it is likely to impact on the findings. We will explore the impact of the level of bias through sensitivity analyses (see ‘Sensitivity analysis’).

Measures of treatment effect

Dichotomous data

We will present results as summary risk ratios and risk differences with 95% confidence intervals for dichotomous data. If statistically significant, we will present the number needed to treat for an additional beneficial or harmful outcome (NNTB/NNTH).

Continuous data

We will use the weighted mean difference for continuous data if outcomes are measured in the same way in all trials. We will use the standardised mean difference to combine data from trials that measure the same outcome using different methods. We will present these data with 95% confidence intervals.

Unit of analysis issues

Randomised trials where participant serves as own control

We will include these trials along with individually randomised trials. We will consider it reasonable to combine the results from both types of study if there is little heterogeneity between the study designs.

Cluster randomised trials

We will include cluster randomised trials in the analyses along with individually randomised trials. We will adjust their sample sizes by means of the methods described in the Cochrane Handbook for Systematic Reviews of Interventions, using an estimate of the intracluster correlation coefficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population (Higgins 2011). If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster randomised trials and individually randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both if there is little heterogeneity between the study designs and an interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely. We will seek statistical advice for this part of the analysis.

We will also acknowledge heterogeneity in the randomisation unit and perform a sensitivity analysis to investigate the effects of the randomisation unit.

Dealing with missing data

For included studies, we will note levels of attrition. We will explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect using sensitivity analyses.

For all outcomes, we will carry out analyses, as far as possible, on an intention‐to‐treat basis (i.e. we will attempt to include all participants randomised to each group in the analyses, and analyse all participants in the group to which they were allocated, regardless of whether or not they received the allocated intervention). The denominator for each outcome in each trial will be the number randomised minus any participants whose outcomes are known to be missing.

Assessment of heterogeneity

We will assess statistical heterogeneity in each meta‐analysis using the I² statistic. We will identify heterogeneity using the following categories: less than 25%, no heterogeneity; 25% to 40%, low heterogeneity; 50% to 74%, moderate heterogeneity; and 75% or greater, high heterogeneity. We will explore substantial heterogeneity (≥ 75%), if identified, using subgroup analyses.

Assessment of reporting biases

Where we suspect reporting bias (see ‘Selective reporting bias’), we will attempt to contact study authors asking them to provide missing outcome data. Where this is not possible, and the missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results using sensitivity analyses.

We will create funnel plots using Review Manager version 5.2 (RevMan 2011) and assess the presence of publication bias by visual inspection of the plots for funnel plot asymmetry. Unfortunately, where the effect measure for dichotomous outcomes is the relative risk (or risk ratio), as is the case for potentially two of the outcomes in this review (skin assessment scores and maternal satisfaction), there is limited evidence to underpin the statistical assessment of funnel plot asymmetry (Higgins 2011). Therefore, we will limit our assessment of funnel plot asymmetry to a visual inspection only.

Data synthesis

Statistical analyses will be performed using the standard methods of the Cochrane Neonatal Review Group. Review Manager version 5.2 (RevMan 2011) will be used for meta‐analyses. We will use fixed‐effect meta‐analyses for combining data where it is reasonable to assume that studies are estimating the same underlying treatment effect (i.e. where trials are examining the same intervention, and the trials’ populations and methods are judged to be sufficiently similar). If there is clinical heterogeneity sufficient to expect that the underlying treatment effects differ between trials, or if we detect substantial statistical heterogeneity (see ‘Assessment of heterogeneity’), we will attempt to explain the heterogeneity identified in the fixed‐effect model based on differences in clinical, quality or other characteristics between studies.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses based on:

1. setting: high‐income countries (gross national income (GNI) per capita $4036 or more) versus low‐income countries (GNI per capita $4035 or less (World Bank 2012));

2. ethnicity: white versus black and minority ethnic;

3. family history of atopic eczema (“at least one of father, mother, or sibling, who has a medical diagnosis of atopic eczema and who has had topical steroid treatment”) versus no family history of atopic eczema.

For fixed‐effect meta‐analyses, we will conduct planned subgroup analyses classifying whole trials by interaction tests as described by Deeks 2001.

Sensitivity analysis

We will perform sensitivity analyses based on trial quality, separating high‐quality trials from trials of lower quality. We will define high quality, for the purposes of this sensitivity analysis, as a trial having adequate allocation concealment and a ‘reasonably expected loss to follow up’ (classified as less than 10%). We will restrict sensitivity analyses to primary outcomes.