Criteria for considering studies for this review
Types of studies
Randomised and quasi-randomised controlled trials (individually or cluster randomised). We will not include studies with a cross-over design.
Types of participants
Newborn infants aged from birth to 28 days with bacteriologically confirmed diagnosis of bacterial meningitis or suspect meningitis. We will include only bacterial meningitis (with the exception of tuberculous meningitis).
Bacteriologically confirmed diagnosis of bacterial meningitis will be defined using CSF microscopy, culture, PCR, or a combination.
Suspect meningitis will be defined as deranged CSF parameters such as leukocyte count greater than 32/mm3 or CSF protein greater than 150 mg/dL or CSF glucose less than 50% of simultaneously determined random blood glucose, in the absence of positive CSF culture.
Types of interventions
Adjunctive parenteral corticosteroid (at any dose and for any duration of treatment). Corticosteroids of interest may include dexamethasone, hydrocortisone, betamethasone and methylprednisolone. Corticosteroids will be administered by the intravenous route.
Appropriate antibiotic therapy alone or in combination with a placebo.
By adjunctive we mean that all the babies in the trial must have had parenteral antibiotics of a class and at a dose that would be considered sufficient for the treatment of neonatal meningitis. Classes of antibiotics allowed will include third-generation cephalosporins, penicillins, vancomycin and aminoglycosides. Penicillins alone or with aminoglycosides and cephalosporins alone or with aminoglycosides and at a dose that will be considered sufficient (doses vary with the drugs used but high doses are generally considered anti-meningitic).
Types of outcome measures
All-cause death until hospital discharge.
Presence of sensorineural deafness at one year of age (this will be assessed by clinical examination and audiometry at one year of age).
Presence of severe neurological deficits or developmental delay between one and two years of age (a neurological deficit will be defined as a functional abnormality of a body area that is observed due to an abnormality in the function of the brain, spinal cord, muscles or nerves. Developmental delay will be defined as any significant lag in a child's physical or motor, cognitive, behavioural, emotional or social development, in comparison with other children of same age and sex within similar environments. Neurological deficits and developmental delay will be assessed using formal evaluation tools). Examples of neurological deficits include mental retardation, cerebral palsy, epilepsy, blindness and behavioural disorders. We will consider evaluation tools such as the Bayley's Infant Scale or the Griffith's Mental Development Scale (for neurodevelopmental deficits), the Gross Motor Functions Scale or the Movement Assessment Battery for Children (for cerebral palsy), Sonken-Silver visual acuity (for blindness), distraction test (for behavioural disorders) and electroencephalography (for epilepsy), all applied between one and two years of age.
All-cause death during first year of life.
Number of patients with seizures at any time.
Number of patients having seizures persisting beyond five days after initiation of treatment.
Fever clearance time (the time between onset of treatment and sustained resolution of fever without recurrence during same illness).
Duration of hospitalisation (in days).
Serious adverse events (leading to death, disability or prolonged hospitalisation), for example, secondary fever and gastrointestinal bleeding. Adverse effects will be defined as unfavourable outcomes that occur during or after the use of an intervention but not necessarily caused by it. Serious adverse events are events that lead to death, disability or prolonged hospitalisation.
Other adverse events.
Incidence of ventriculitis (neuroimaging with evidence of intraventricular debris, pus and enhanced ventricular lining during hospitalisation).
Incidence of hydrocephalus (clinically diagnosed with or without ultrasound confirmation of ventricular dilation occurring during hospitalisation or within one year of treatment).
Incidence of SIADH at one month post treatment (rapid weight gain, decreased urine output, serum sodium less than 130 mmol/L, plasma osmolality less than 270 mOsm/kg, urinary osmolality greater than 100 mOsm/kg and urinary sodium greater than 40 mmol/L during hospitalisation).
Incidence of bleeding diatheses at one month post treatment (external bleeding including oozing from puncture sites, purpura and petechiae, as well as evidence of internal bleeding such as haematuria and haematemesis occurring during hospitalisation).
Search methods for identification of studies
We will contact the Neonatal Review Group Trials Search Co-ordinator to search the review group's trials registry. We will search the Cochrane Neonatal Group's specialised register, the Cochrane Central Register of Controlled Trials (CENTRAL, The Cochrane Library), MEDLINE (1966 to date); African Index Medicus (up to date), CINAHL (up to date), EMBASE (up to date), LILACS (up to date) and the Science Citation Index (up to date). We will also search the metaRegister of Controlled Trials (mRCT) to identify some completed/yet unpublished and ongoing trials. We will maintain no language restrictions. If we identify a study in abstract form only, we will evaluate it for possible inclusion in the review and will attempt to contact the authors for more information to either include or exclude the study. We will perform a handsearch of the reference lists of articles for which the full text is obtained.
We will use the search strategy provided in the guidelines of the Cochrane Neonatal Review Group. The key words will include [CORTICOSTEROIDS] OR [STEROIDS] OR [DEXAMETHASONE] OR [METHYLPREDNISOLONE] OR [BETAMETHASONE] OR [HYDROCORTISONE] AND [NEONATAL] OR [NEWBORN] OR [NEONATES] OR [INFANTS] AND [MENINGITIS] AND [BACTERIAL] OR [PYOGENIC] NOT [TUBERCULOUS] AND [CLINICAL TRIAL] OR [RANDOMIZED CONTROLLED TRIAL].
Searching other resources
We will contact researchers in the field to ask for knowledge of any ongoing studies and will handsearch the abstracts of neonatology conferences to identify further trials.
Data collection and analysis
Selection of studies
Two review authors (TAO and CCO) will independently screen the results (titles and abstracts) of the literature search for potentially relevant trials. We will retrieve full reports of the potentially relevant trials and independently determine if they meet the review inclusion criteria using a pre-tested eligibility form. For each step of the review, we will resolve contentious issues by discussion. We will consult an Editor within the Cochrane Neonatal Group, where necessary. We will also attempt to contact trial authors for further information if trial eligibility is unclear. We will list all excluded studies, along with the reason for excluding them. We will ensure that trials with multiple publications are included only once, but if we find that multiple publications include different but relevant outcomes, we will include all the publications in the review. All different references from the same study will be included under the main reference.
Data extraction and management
Two review authors (TAO and CCO) will independently extract data using a pre-tested data extraction form. One review author (CCO) will enter the data into Review Manager 5.1 (RevMan 2011 while a second review author (TAO) will cross-check the data for completeness and accuracy. Data will be extracted from the number of participants randomised and number analysed in each group for each reported outcome.
We will extract data for dichotomous outcomes by recording the total number of participants randomised, number of participants experiencing the events and number of participants in each treatment group.
For continuous outcomes, we will extract the number of participants for each treatment arm, arithmetic means and standard deviations (SDs). If we encounter data with skewed distribution, where the data have been reported as geometric means, we will extract geometric means and SDs on the log scale or as medians and ranges if medians have been used. For rate and count outcomes (such as participants with outcomes that occur more than once over the period of trial), we will extract the number of events or episodes experienced in each trial arm and person-time over which the events were experienced for each group. We will extract hazard ratios and SDs for time-to-event outcomes. We will extract data on reported adverse events.
We will attempt to contact the trial authors where the relevant details were not recorded or were unclear. If there are disagreements with regard to data extraction, we will resolve them by discussion and asking for the opinion of an Editor in the Neonatal Group.
Assessment of risk of bias in included studies
We will independently assess risk of bias for every eligible study using the guidelines provided in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).
Disagreements will be resolved through discussions.
We will independently assess the risk of bias within each included study in relation to the following five domains (allocation sequence generation, allocation concealment, blinding, handling of incomplete outcome data and selective outcome reporting) with ratings of 'Yes' (low risk of bias), 'No' (high risk of bias) and 'Unclear' (uncertain risk of bias).
Details of specific assessments are as outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).
(1) Allocation sequence generation
We will describe, for each included study, the method used to generate the allocation sequence to allow an assessment of whether it should produce comparable groups.
The methods will be graded as follows:
low risk of bias (truly random processes such as the use of table of randomisation or computer-generated random numbers);
high risk of bias (non-random processes such as use of hospital record numbers or dates of birth);
unclear risk of bias.
(2) Allocation concealment
We will describe for each included study, the method used to conceal allocation to interventions prior to assignment and will assess whether intervention allocation could have been predicted before or changed after recruitment. The methods will be graded as follows:
low risk of bias;
high risk of bias;
unclear risk of bias.
(3) Blinding of participants and researchers
We will describe for each included study, the methods used to blind study participants and researchers from knowledge of which intervention a participant received. Blinded studies or studies in which non-blinding was not likely to affect results significantly will be classified as low risk of bias. Non-blinded studies will be classified as high risk of bias.
4) Incomplete outcome data
We will describe for each included study, the methods used to account for incomplete outcome data, with regard to the amount, nature and handling of incomplete outcome data. In instances where studies do not report complete outcome data, we will attempt to obtain missing data by contacting the study authors. We will extract and report on data on attrition and exclusions as well as the numbers involved (compared with total randomised), reasons for attrition/exclusion where reported or obtained from investigators, and any re-inclusions in analyses performed by review authors. Unbiased follow-up will be taken as when at least 80% of the participants can be continued to be followed up. Based upon this, we will judge whether the researchers dealt with incomplete data. We will rate as follows: 'yes' (low risk of bias); 'no' (high risk of bias) and 'unclear' (uncertain risk of bias).
5. Selective outcome reporting
We will attempt to assess the possibility of selective outcome reporting by investigators in the included trials, where available we will also attempt to look at study protocols; based upon this, we will judge whether reports of the study were free from suggestion of selective outcome reporting.
We will rate as follows: 'yes' (low risk of bias), 'no' (high risk of bias) and 'unclear' (uncertain risk of bias).
We will explore other sources of bias, particularly the sources of funding of the included studies and other study peculiarities.
Measures of treatment effect
If means and SDs are available, continuous data will be analysed. We will extract and utilise this for the analysis irrespective of provision of mean and SD if mean difference is provided. We will be interested in post intervention values. We will re-calculate the SD in instances where the standard error is reported. We will extract data from studies that reported adequately on skewed continuous data as medians rather than means. We will report these data separately where appropriate. We will calculate the weighted mean difference (WMD) and 95% confidence interval (CI) for continuous data.
We will analyse binary outcomes by calculating the risk ratio (RR), risk difference (RD) and number needed to treat for an additional beneficial outcome (NNTB) and number needed to treat for an additional harmful outcome (NNTH) with 95% CIs.
Unit of analysis issues
We will describe, for each included study, the observations on participants at selected time points. We will analyse follow-up data available at the point of discharge from the hospital as well as at the age of one month, three months, six months and one year as we will be assessing some of the outcomes at these different time points. We will adjust for clustering by applying the intracluster correlation coefficient if cluster trials are identified.
Dealing with missing data
When necessary, we will attempt to contact the study author(s) to supply any unreported data (e.g. group means and SDs, details of dropouts, and details of interventions received by the control group). If a study reports outcomes only for participants completing the trial or only for participants who followed the protocol, authors will be contacted and asked to provide additional information to facilitate an intention-to-treat analysis and in instances where this is not possible we will perform a complete case analysis.
Assessment of heterogeneity
Statistical heterogeneity will be assessed by examining the I2 statistic (Higgins 2002; Higgins 2003), a quantity that describes approximately the proportion of total variation that is due to variation between studies. In addition, a Chi2 test of homogeneity at 10% level of statistical significance will be employed to determine the strength of evidence against the hypothesis that all studies come from the same population. As a rough guide, an I2 statistic between 0% and 50% will represent mild heterogeneity, 51% to 75% will represent moderate heterogeneity and above 75% will indicates considerable heterogeneity. We will inspect forest plots, as poor overlap may be due to significant heterogeneity.
Assessment of reporting biases
We will prepare funnel plots (estimated treatment effects against their standard error) to explore publication bias if there are more than 10 trials in a comparison. Asymmetry could be due to publication bias, but can also be due to a relationship between trial size and effect size.
We will conduct meta-analyses for trials with similar characteristics. We will carry out an intention-to-treat analysis or carry out a complete case analysis where there is loss to follow up. We will use the fixed-effect model and present all our results with 95% CI. We will calculate the NNTB, NNTH, WMD and 95% CIs for our continuous outcomes, and RR and RD with 95% CIs for our dichotomous outcomes.
Subgroup analysis and investigation of heterogeneity
We will conduct subgroup analyses to assess the benefit or otherwise of adjunctive corticosteroid treatment.
We will perform subgroup analyses to address:
the efficacy of adjuvant corticosteroids in infants with gestational age < 37 weeks and those ≥ 37 weeks;
the efficacy of corticosteroids as an adjuvant treatment in different antibiotic classes (comparison will be made for penicillins with or without aminoglycosides versus cephalosporins with or without aminoglycosides);
the efficacy of adjuvant corticosteroids based on causative bacterial agent (comparison will be made for GBS and other Gram-positive bacteria versus Gram-negative bacteria);
impact of the time of initiation of adjunctive corticosteroid treatment (comparison will be made for pre-antibiotic (up to one hour prior to the commencement of antibiotics) and post antibiotic (simultaneously with antibiotics or after the commencement of antibiotics));
impact of the duration of adjunctive corticosteroid treatment on the outcome of neonatal bacterial meningitis (comparison will be made for duration less than four days and four days or more);
impact of corticosteroids on the outcomes for studies conducted in developed countries versus developing countries;
impact of corticosteroids on the outcomes among infants with confirmed meningitis (positive CSF culture or PCR) versus suspect meningitis (deranged cellular or chemical constituents of the CSF without positive CSF culture or PCR).
We will assess important clinical heterogeneity by comparing the distribution of important clinical heterogeneity factors (study participants, study setting, type of intervention and co-intervention, and baseline antibiotic treatment) and methodological heterogeneity factors (randomisation, allocation concealment, blinding of outcome assessment, losses to follow up).
We will conduct sensitivity analyses to explore the effect of the methodological quality of the trials, checking to ascertain if studies with a high risk of bias overestimate the effect of treatment.