Systemic corticosteroid regimens for prevention of bronchopulmonary dysplasia in preterm infants

  • Protocol
  • Intervention



This is the protocol for a review and there is no abstract. The objectives are as follows:

To assess the effects of different corticosteroid regimens on mortality, pulmonary morbidity and neurodevelopmental outcome in very low birth weight (VLBW) infants.


Description of the condition

The first description of bronchopulmonary dysplasia (BPD) by Northway et al. in 1967 was one of severe lung injury in relatively mature preterm infants who were ventilated with high pressures and high concentrations of oxygen before the advent of surfactant therapy (Northway 1967). This so-called 'classical' BPD is characterized by profound lung parenchymal inflammation, fibrosis and muscle hypertrophy and diffuse airway damage (O'Brodovich 1985). Treatment and survival of the very young has led to a new pattern of lung injury (Jobe 1999; Coalson 2006). This so-called 'new' BPD is mainly seen in very preterm infants with gestational ages less than 30 weeks. It is characterized by an arrest in lung development with fewer and larger alveoli, and less striking fibrosis and inflammation (Husain 1998). Due to the recognition of this new entity, the timing of assessment of BPD diagnosis shifted from 28 days' postnatal age (PNA) to 36 weeks' postmenstrual age (PMA) (Bancalari 2006). Cohort studies showed that the latter timing of diagnosis determined the long-term pulmonary and neurological outcome superior to the old definition (Ehrenkranz 2005).

BPD, defined as oxygen dependency at 36 weeks' PMA, remains an important complication of preterm birth with a reported incidence of 23% to 73% depending on the gestational age (Stoll 2010). BPD is characterized by prolonged respiratory support, compromised lung function and recurrent respiratory infections during the first years of life. Furthermore, BPD is considered an independent risk factor for neurodevelopmental impairment (Walsh 2005; Short 2007).

BPD is considered a multifactorial disease. Besides genetic susceptibility, intrauterine growth restriction, nutritional deficits, direct mechanical injury caused by artificial ventilation and oxygen toxicity, pulmonary inflammation has been identified as an important cause in the development of BPD (Carlton 1997; Ferreira 2000; Jobe 2001). Corticosteroids have a strong anti-inflammatory effect, making them an ideal candidate to attenuate the inflammatory response associated with BPD.

Description of the intervention

Since the 1980s, several randomized controlled trials (RCTs) have investigated the use of corticosteroids, in particular dexamethasone, as a means to reduce the incidence of BPD. Some of these trials started corticosteroid therapy in the first week of life (early), with the aim of preventing progression of the initial acute inflammatory response to BPD (Yeh 1997). Others used corticosteroid therapy in infants who had evolving BPD, starting administration either moderately early (7 to 14 days) or delayed (> three weeks) after birth (CDTG 1991; Durand 1995).

The current Cochrane reviews of the placebo-controlled RCTs clearly show that systemic corticosteroids, mainly dexamethasone, significantly reduce the incidence of BPD and the combined outcome death or BPD in ventilated preterm infants, independent of the time of postnatal administration (Halliday 2009; Halliday 2010). However, at the end of the 1990s, the first reports on long-term neurodevelopmental outcome were published, showing that early postnatal systemic dexamethasone treatment is associated with an increased risk of abnormal neurological development (Yeh 1998; O'Shea 1999).

In response to these reports, the American Academy of Pediatrics, the Canadian Paediatric Society and the European Association of Perinatal Medicine concluded that routine use of systemic dexamethasone in the treatment of evolving BPD can no longer be recommended until further research has established the optimal type, dose and timing of corticosteroid therapy (Halliday 2001; AAP 2002; Watterberg 2010). Following these statements, observational reports have shown a sharp decline in the use of postnatal corticosteroids, as well as the use of markedly reduced cumulative doses, delayed initiation of treatment and changing to alternative corticosteroids as hydrocortisone (Kaempf 2003; Shinwell 2003; Walsh 2006).

How the intervention might work

In order to reduce the associated adverse short-term and long-term neurological effects of postnatal dexamethasone, several alternatives have been studied, as well as alterations in dosage regimens regarding cumulative dose, duration and timing of initiation to improve the benefit:risk ratio.

  1. Alternative corticosteroids: The concerns on the long-term neurodevelopmental outcomes following dexamethasone administration led to the introduction of alternative anti-inflammatory corticosteroids, such as hydrocortisone. Animal studies have suggested that, in contrast to dexamethasone, hydrocortisone has no detrimental effect on the brain (Huang 2007). Historical cohort studies have suggested that hydrocortisone treatment is equally effective in reducing death or BPD compared with dexamethasone-treated infants without causing an increased risk of adverse neurological outcome (van der Heide-Jalving 2003; Karemaker 2006; Rademaker 2007; Lodygensky 2005). To date, pooled data on placebo-controlled trials investigating a low hydrocortisone dose initiating at an early treatment onset showed no reduction in the incidence of death or BPD (Doyle 2010). Only one of these trials reported long-term follow-up, showing no differences in adverse neurodevelopmental sequelae (Watterberg 2007). No placebo-controlled randomized trials have investigated the use of hydrocortisone after the first week in life in ventilator-dependent preterm infants.

  2. Lowering the corticosteroid dose and duration: In line with the current opinion of postnatal corticosteroids being 'misguided rockets', clinicians have started to use lower dosage schedules of dexamethasone. The available reviews on placebo-controlled trials of postnatal corticosteroids stacked information from trials with tremendous clinical heterogeneity in their cumulative dose and duration of therapy (Halliday 2010). Subgroup analyses using this clinical heterogeneity by dividing the different trials according to the used cumulative dexamethasone dose showed that higher dexamethasone doses reduces the typical risk ratio (TRR) for the combined outcome mortality or BPD, with the largest effect in trials using a cumulative dose above 4 mg/kg (Onland 2009). No effect was found of doses on the risk of neurodevelopmental sequelae; however, in the moderately early treatment studies the risk of mortality or cerebral palsy (CP) significantly decreased when using a higher cumulative dose (Onland 2009).

  3. Postponing initiation of therapy: Besides lowering the cumulative dose, clinicians postpone the administration of postnatal corticosteroids until the third or fourth week of postnatal life. However, placebo-controlled trials administrating dexamethasone after the first week of life show a lower number needed to treat for an additional beneficial effect (NNTB) for reducing BPD in favour of earlier administration and, although not significant, a beneficial effect on long-term neurodevelopmental outcome (Schmidt 2008; Onland 2009). At present, we can only speculate on the possible mechanisms for this time-dependent effect of dexamethasone therapy on neurodevelopmental outcome. First, as suggested by animal data, the direct effect (beneficial or harmful) of dexamethasone on the brain might differ depending on the PNA of exposure (Tuor 1995). Second, the effect of dexamethasone on the pulmonary condition and outcome (i.e. BPD) may also indirectly have an effect on the neurodevelopmental outcome. Protracted mechanical ventilation has been shown to be an independent risk factor for neurodevelopmental sequelae (Walsh 2005). As starting dexamethasone in the moderately early time frame will almost certainly reduce the time on mechanical ventilation compared to delayed treatment, it may thus reduce the risk for CP. One study in preterm baboons showed that a difference as small as five days of mechanical ventilation already results in decreased brain growth and the presence of subtle brain injury . In addition to mechanical ventilation, BPD itself is an important independent risk factor for CP (Majnemer 2000). Therefore, reducing the incidence of BPD, when starting dexamethasone treatment moderately early, might, in part, explain the time-dependent (moderately early vs. delayed) effect of dexamethasone on CP. Considering these mechanisms in combination, it might well be that a direct negative effect of dexamethasone on the brain is overridden by the indirect beneficial effect mediated via a reduction in time on mechanical ventilation and the incidence of BPD. This concept has also been shown by one systematic review using meta-regression showing that the adverse effects of moderately early or late administrated postnatal corticosteroids on long-term neurodevelopmental outcome might be modified by the BPD risk (Doyle 2005).

  4. Pulse dose administration: To avoid the complications and side effects associated with long-term continuous corticosteroid use, an alternative method might be to prescribe dexamethasone in a pulse regimen using the dexamethasone-free interval to minimize the direct toxic effect of dexamethasone on brain growth, without reducing the pulmonary benefits. One placebo-controlled trial showed that this regimen with pulse doses resulted in improvement in pulmonary outcome without clinically significant side effects (Brozanski 1995).

  5. Individualized tailored regimen: Another approach to avoid the associated side effects on short- and long-term outcomes, is aiming to tailor the administered dose individually to the infant's respiratory status, thus having the optimal respiratory benefits without having the adverse effects (Bloomfield 1998).

However, the effects of any these interventions on pulmonary benefits and short- and long-term adverse effects remains unclear.

Why it is important to do this review

The international neonatal community has discarded the use of early postnatal glucocorticoids completely for the above reasons. Regarding the use of moderately early or late postnatal systemic corticosteroids, clinicians encounter a dilemma facing those patients at high risk of BPD, since BPD itself is associated with an increased risk of adverse neurological outcome (Ehrenkranz 2005).

It is unknown whether both the beneficial and adverse treatment effects of postnatal corticosteroids can be modulated by the various different dosing regimens described above. Despite the aforementioned concerns on the long-term neurodevelopmental sequelae, corticosteroids are still used in approximately 16% of the preterm infants (Costeloe 2012). Therefore, clinicians are in doubt as to what the correct drug, cumulative dose, duration and timing of therapy is in terms of the optimal balance between beneficial and adverse effects. Answering these open questions is important as some studies have suggested that the restricted use of postnatal corticosteroids has resulted in an increase of the incidence of BPD (Shinwell 2007; Yoder 2009; Cheong 2013).


To assess the effects of different corticosteroid regimens on mortality, pulmonary morbidity and neurodevelopmental outcome in very low birth weight (VLBW) infants.


Criteria for considering studies for this review

Types of studies

Randomized controlled or quasi-randomized and cluster-randomized trials comparing two or more different regimens of systemic corticosteroids in VLBW infants at risk for BPD. We will exclude studies investigating the effects of one regimen of systemic corticosteroids versus a placebo arm or studies using inhalation corticosteroids.

Types of participants

VLBW infants at risk for BPD, as defined by the original trialists.

Types of interventions

Trials will include infants randomized to treatment with two different regimens of systemic corticosteroids. The following types of intervention will be eligible:

  1. an alternative corticosteroid (e.g. hydrocortisone) as the experimental arm versus another type of corticosteroid (e.g. dexamethasone) as the control arm. Any type of corticosteroid in either arms will be eligible;

  2. lower cumulative corticosteroid dosage (experimental arm) versus higher cumulative corticosteroid dosage (control arm). Both arms of the identified trials will be categorized according to the cumulative dosage investigated; 'low' being less than 2 mg/kg; 'moderate' being between 2 and 4 mg/kg; and 'high' using a cumulative dosage greater than 4 mg/kg. We will include studies investigating the effects of low versus moderate dosage regimen, as well as studies comparing moderate versus high dosage regimen, and, if identified, a high versus low dosage. Although arbitrary, these cut-off values were chosen given the results of the systematic review of placebo-controlled trials (Onland 2009);

  3. later (experimental arm) versus earlier (control arm) initiation of therapy. We will categorize both arms of the identified trials according to the investigated timing of initiation; 'early' being less than 7 days' PNA; 'moderately early' being between 7 and 21 days' PNA; and 'delayed' being greater than 21 days' PNA. Studies investigating the effects of early versus moderately early onset are to be pooled, as well as studies comparing moderately early versus delayed onset, and if identified early versus delayed timing of onset. This arbitrary cut-off point has been chosen according to the original Cochrane reviews on placebo-controlled trials (Halliday 2003a; Halliday 2003b; Halliday 2003c);

  4. pulse dosage regimen (experimental arm) versus continuous dosage regimen (control arm); and

  5. individually tailored regimens (experimental arm) based on pulmonary response defined by the original trialists versus a standardized (a pre-determined schedule administered to every infant) dosage regimen (control arm).

Types of outcome measures

Two review authors (WO and ADJ) will independently extract the following outcome parameters for each study.

Primary outcomes
  • Combined outcome mortality or BPD at 36 weeks' PMA (BPD defined as oxygen dependency at 36 weeks' PMA).

Secondary outcomes
  • Death at 28 days' PNA, 36 weeks' PMA, hospital discharge and during the first year of life.

  • BPD (defined by the need for supplemental oxygen) at 28 days' PNA and 36 weeks' PMA.

  • Failure to extubate at days three and seven after initiating therapy and at the latest reported time point.

  • Days of mechanical ventilation.

  • Days of supplemental oxygen.

  • Hypertension, defined as more than two standard deviations (SD) according to local protocols.

  • Hyperglycaemia, defined as greater than 8.3 mmol/L or requiring insulin therapy, or both.

  • Culture-confirmed and clinical-suspected infection.

  • Gastrointestinal bleeding or perforation (spontaneous intestinal perforation (SIP)).

  • Necrotizing enterocolitis, following Bells' stages.

  • Patent ductus arteriosus (PDA), according to trial protocol and requiring therapy.

  • Intraventricular haemorrhage (IVH), any and severe grades.

  • Periventricular leukomalacia (PVL).

  • Cardiac hypertrophy.

  • Adrenal suppression.

  • Rescue treatment with open-label corticosteroids within or outside the study period.

  • Retinopathy of prematurity (ROP), any and severe stages.

  • Long-term neurodevelopmental sequelae, assessed after at least one year corrected gestational age (CGA) and before a CGA of four years, and at the latest reported time point, including CP and Bayley's Scales of Infant Development (Mental Development Index, MDI).

  • Blindness.

  • Deafness.

Search methods for identification of studies

We will use the search strategy of the Cochrane Neonatal Review Group to identify studies with electronic searches using the Medical Subject Heading terms (MeSH) and text words: 'adrenal cortex hormones'OR 'dexamethasone'OR 'betamethasone'OR 'hydrocortisone'OR 'prednisolone'OR 'methylprednisolone'OR 'steroids'OR 'corticosteroids'OR 'glucocorticoids'and Limits: randomised controlled trials AND infant, newborn. We will apply no language restrictions in the search strategy. We will contact original authors of all studies to confirm details of reported follow-up studies or to obtain information about long-term follow-up where none are reported.

Electronic searches

We will identify clinical trials by electronic searches of the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE (from 1966 onwards), EMBASE (from 1974 onwards) and CINAHL (from 1982 onwards).

Searching other resources

We will handsearch reference lists of published trials and review articles, and the abstracts of the Pediatric Academic Societies and the European Society for Paediatric Research (from 1990 onwards).

Data collection and analysis

Selection of studies

Two review authors (WO and ADJ) will classify the relevant citations found by the database searches into three groups: 'clearly an RCT', 'clearly not an RCT' and 'possibly an RCT'. We will do a full-text review on all except those classified as 'clearly not a RCT'. We will resolve any disagreements by consensus.

Data extraction and management

Two review authors (WO and ADJ) will independently extract the following data for each study using a pre-defined data sheet, in addition to the pre-defined outcome measurements: patient characteristics (such as birth weight, gestational age, gender), number of patients randomized, treatment with antenatal corticosteroids and postnatal surfactant; type of corticosteroid and regimens (PNA at start, duration of therapy, cumulative dose, dose adjusted to actual weight during course), and the incidence of open-label (outside the study protocol) use of corticosteroids in both arms of the studies. We will ask the original investigators of the included RCTs to confirm whether the data extraction was accurate and, where necessary, to provide additional (unpublished) data.

Assessment of risk of bias in included studies

We will assess the methodological qualities of the included trials using the standard methods of the Cochrane Neonatal Review Group. The following headings and associated questions (based on the questions in the 'Risk of bias' table) will be evaluated by two review authors (WO and ADJ) and entered into the 'Risk of bias' table:

  • Adequate sequence generation? For each included study, we will categorize the risk of selection bias as:

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

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

    • unclear risk - no or unclear information provided.

  • Allocation concealment? For each included study, we will categorize the risk of bias regarding allocation concealment as:

    • low risk - adequate (e.g. telephone or central randomizations; consecutively numbered sealed opaque envelopes);

    • high risk - inadequate (open random allocation; unsealed or non-opaque envelopes, alternation; date of birth);

    • unclear risk - no or unclear information provided.

  • Blinding?

    • Performance bias? For each included study, we will categorize the methods used to blind study personnel from knowledge of which intervention a participant received. (As our study population will consist of neonates they would all be blinded to the study intervention.)

      • low risk - adequate for personnel (a placebo that could not be distinguished from the active drug was used in the control group);

      • high risk - inadequate - personnel aware of group assignment;

      • unclear risk - no or unclear information provided.

    • Detection bias? For each included study, we will categorize the methods used to blind outcome assessors from knowledge of which intervention a participant received. (As our study population will consist of neonates they would all be blinded to the study intervention.) Blinding will be assessed separately for different outcomes or classes of outcomes. We will categorize the methods used with regards to detection bias as:

      • low risk - adequate; follow-up was performed with assessors blinded to group;

      • high risk - inadequate; assessors at follow-up were aware of group assignment;

      • unclear risk - no or unclear information provided..

  • Incomplete data addressed (attrition bias)? For each included study and for each outcome, we will describe the completeness of data including attrition and exclusions from the analysis. We will note whether attrition and exclusions were reported, the numbers included in the analysis at each stage (compared with the total randomized 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 supplied by the trial authors, we will re-include missing data in the analyses. We will categorize the methods with respect to the risk attrition bias as:

    • low risk - adequate (<10% missing data);

    • high risk - inadequate (>10% missing data);

    • unclear risk - no or unclear information provided.

  • Free of selective reporting (reporting bias)? For each included study, we will describe how we investigated the risk of selective outcome reporting bias and what we found. We will assess the methods as:

    • low risk - adequate (where it is clear that all of the study's pre-specified outcomes and all expected outcomes of interest to the review have been reported);

    • high risk - inadequate (where not all the study's pre-specified outcomes have been reported; one or more reported primary outcomes were not pre-specified; 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 risk - no or unclear information provided (the study protocol was not available).

  • Free of other bias? For each included study, we will describe any important concerns we have about other possible sources of bias (e.g. whether there was a potential source of bias related to the specific study design or whether the trial was stopped early due to some data-dependent process). We will assess whether each study was free of other problems that could put it at risk of bias as:

    • low risk - no concerns of other bias raised;

    • high risk - concerns raised about multiple looks at the data with the results made known to the investigators, difference in number of patients enrolled in abstract and final publications of the paper;

    • unclear - concerns raised about potential sources of bias that could not be verified by contacting the authors.

Overall risk of bias

We will make explicit judgments 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). 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 undertaking sensitivity analyses - see Sensitivity analysis. If necessary, we will ask the original investigators to provide additional information.

Measures of treatment effect

We will conduct data management using the Cochrane statistical package, Review Manager 5 (RevMan 2012). We will calculate treatment effect estimates, where possible, for the dichotomous outcomes in all individual trials expressed as risk ratio (RR) and risk difference (RD), all with a 95% confidence interval (CI). For the continuous outcomes reported in the individual studies the mean values for treatment and control groups will use the SD. If median and range is given in the individual studies, and the study authors are not able to provide the mean value and variance from the original data set, they will be calculated according to the method described by Hozo et al. (Hozo 2005). We will calculate the NNTB and number needed to treat for an additional harmful outcome (NNTH) for each different outcome in case of significance of that outcome. All analyses will be done on an intention-to-treat basis.

Unit of analysis issues

If cluster-randomized trials are included in the analyses, we will adjust their sample sizes using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

Dealing with missing data

We will ask the study author of the included RCTs to confirm whether the data extraction was accurate and, where necessary, to provide additional (unpublished) data.

Assessment of heterogeneity

We will assess heterogeneity between trials by inspecting the forest plots and quantifying the impact of heterogeneity using the I2 statistic, using the following categories as defined by the Cochrane Neonatal Review Group:

  • less than 25%: no heterogeneity;

  • 25% to 49%: low heterogeneity;

  • 50% to 74%: moderate heterogeneity;

  • 75% or greater: high heterogeneity.

We will explore possible causes of statistical heterogeneity using pre-specified subgroup analysis (e.g. differences in intervention regimens).

Assessment of reporting biases

We plan to use funnel plots to assess possible reporting or publication biases.

Data synthesis

We will perform meta-analysis of the extracted data using the standard methods of The Cochrane Collaboration and Review Manager 5 (RevMan 2012). Treatment effects for the dichotomous outcomes will be expressed as TRR with a 95% CI, typical risk difference (TRD), and NNTBs or NNTHs in case of significance. We will use mean differences (MD) for continuous outcomes. In case of variance of outcome measures (with different SD) measuring the same outcome, we will calculate standardized mean differences (SMD) in the meta-analysis. We will use the fixed-effect model for the meta-analyses.

Subgroup analysis and investigation of heterogeneity

If we identify substantial heterogeneity, we will investigate it using subgroup analyses and sensitivity analyses, and, if not appropriate, reconsider whether an overall summary is meaningful at all. We plan to carry out the following subgroup analysis:

  • gestational age using an arbitrary cut-off point of 26 weeks;

  • the degree of illness at the start of treatment as defined by mean respiratory index or fractional inspired oxygen if available at trial entry;

  • ventilated versus not ventilated neonates at study entry;

  • trials allowing use of open-label corticosteroids during the study period, by dividing the individual trials according to the percentage of open-label corticosteroids in the experimental arm, using arbitrary cut-off points of less than 30%, 30% to 50%, and greater than 50%; and,

  • trials investigating two (or more) of the main comparisons will be analyzed in both comparisons in subgroups. For example, if a study investigates one arm administered hydrocortisone at an early initiation versus a dexamethasone regimen at a later treatment onset, this study will be analysed in both comparisons in subgroups.

Sensitivity analysis

We will perform sensitivity analyses when trials are judged with a high risk of bias to assess the effect of the bias on the meta-analysis.

Contributions of authors

Dr Onland has full access to all of the data in the study and will take responsibility for the integrity of the data and the accuracy of the data analysis.

Study concept and design: Onland, van Kaam.

Acquisition of data: Onland, De Jaegere.

Analysis and interpretation of data: Onland, De Jaegere, Offringa, van Kaam.

Drafting of the manuscript: Onland.

Critical revision of the manuscript for important intellectual content: Onland, De Jaegere, Offringa, van Kaam.

Statistical analysis: Onland, De Jaegere.

Study supervision: Offringa, van Kaam.

Declarations of interest

No financial disclosure to be declared. No potential conflicts of interest known.

Sources of support

Internal sources

  • No sources of support supplied

External sources

  • Eunice Kennedy Shriver National Institute of Child Health and Human Development National Institutes of Health, USA.

    Editorial support of the Cochrane Neonatal Review Group has been funded with federal funds from the Eunice Kennedy Shriver National Institute of Child Health and Human Development National Institutes of Health, Department of Health and Human Services, USA, under Contract No. HHSN275201100016C


Part of this systematic review on one of the comparisons has been published before (Onland 2008).