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. 2018 Nov 6;2018(11):CD013158. doi: 10.1002/14651858.CD013158

Surfactant therapy guided by tests for lung maturity in preterm infants at risk of respiratory distress syndrome

Colby R Kearl 1, Leslie Young 2, Roger Soll 2,✉
PMCID: PMC6516810

Abstract

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

To assess the effects of surfactant treatment guided by rapid tests for surfactant deficiency in preterm infants at risk for or having RDS.

Comparison 1: In preterm infants at risk for RDS, does surfactant treatment guided by rapid tests for surfactant deficiency compared to prophylactic surfactant administration to all high‐risk infants minimize the need for surfactant treatment and prevent bronchopulmonary dysplasia and mortality?

Comparison 2: In preterm infants who require early respiratory support, does surfactant treatment guided by rapid tests for surfactant deficiency compared to surfactant therapy provided to infants with RDS diagnosed on clinical and radiologic criteria minimize the need for surfactant treatment and prevent bronchopulmonary dysplasia and mortality?

Planned subgroup analysis: gestational age, disease severity, timing of testing and treatment, surfactant preparation, exposure to antenatal steroids.

Background

Description of the condition

Respiratory distress syndrome (RDS), previously known as hyaline membrane disease, occurs in newborns when pulmonary surfactant is deficient or dysfunctional (Avery 1959). Pulmonary surfactant is is composed of both proteins and phospholipids The phospholipids, primarily dipalmitoylphosphatidylcholine (DPPC), act to decrease the alveolar surface tension and thus prevent end expiratory atelectasis. The proteins aid in spreading and adsorption at the alveolar surface (Halliday 2008). Surfactant is made by type II pneumocytes and transported to the alveolar surface as lamellar bodies (Verder 2011). The maturation of type II pneumocytes occurs in the later stages of fetal development. Respiratory distress syndrome is thus primarily a disease of preterm infants. However, full‐term infants may present with RDS due to dysfunctional surfactant secondary to genetic mutations in genes such as surfactant protein B or C (SP‐B and SP‐C), or phospholipid transporter (ABCA3) (Wert 2009).

Infants with RDS present with early‐onset respiratory distress. Clinical signs often include intercostal retractions, grunting, and nasal flaring necessitating supplemental oxygen (Bancalari 2012). Further evaluation often reveals classic reticulogranular findings on chest radiograph. However, such radiologic and clinical signs may be masked in infants who are quickly intubated and on ventilatory support. Furthermore, extremely low birth weight infants often present with similar signs of respiratory distress, although the underlining cause may not necessarily be due to surfactant deficiency but rather poor postnatal adaptation, central respiratory depression, and lung inflammation secondary to chorioamnionitis (Bancalari 2012; Laughon 2009; Watterberg 1996). The diagnosis of RDS based on classic respiratory distress and radiographic evidence has resulted in significant diagnostic variation among providers (Fanaroff 2007; Stoll 2010).

There has been significant advancement in the treatment of RDS. Initial treatment focused on the administration of animal‐derived exogenous surfactant (Fujiwara 1980). Further research introduced synthetic surfactants. Research continues to address timing, frequency of dosing, and route of administration of exogenous surfactant. In addition to treatment with exogenous surfactant, maternal use of steroids during fetal development has been shown to promote fetal lung development and decrease the incidence of RDS once born (Robertson 1993). Advancement in respiratory support has allowed for early continuous distending pressure, which has decreased the need for prophylactic surfactant administration (Bahadue 2012; Chernick 1973).

Description of the intervention

Administration of various exogenous surfactant preparations has been shown to decrease lung injury and pneumothorax and improve survival (Jobe 1993; Soll 1997; Soll 1998). Surfactant products include animal‐derived surfactants, as well as protein‐ and non‐protein‐containing synthetic surfactants (Ardell 2015; Lasalvia 2017; Pfister 2007; Pfister 2009; Seger 2009).

Exogenous surfactant treatment strategies include prophylactic, early, or selective administration. Prophylactic administration is the immediate treatment of newborns at risk of RDS (Rojas‐Reyes 2012; Soll 2010). This could occur before (pre‐ventilatory) or after (postventilatory) the first breath. Early administration is the use of exogenous surfactant in the first two hours of life for infants who are intubated for respiratory distress (Bahadue 2012; Stevens 2007). Selective treatment or rescue administration occurs only when the intubated newborn has developed symptoms of RDS (Rojas‐Reyes 2012). Such symptoms included increased fraction of inspired oxygen (FiO2) requirement (frequently defined as 0.4) or mean airway pressure greater than 7 cmH2O.

Exogenous surfactant therapy is administered in several different ways. These include thin endotracheal tube, intrapartum pharyngeal instillation, INSURE (INtubation‐SURfactant‐Extubation), and minimally invasive surfactant therapy (MIST), also known as non‐invasive surfactant therapy (NIST) (Abdel‐Latif 2011; Abdel‐Latif 2012; Abdel‐Latif 2015).

Several tests are used to determine surfactant sufficiency after birth. The most prominent bedside tests are lamellar body counts, click test, and the stable microbubble test (Fiori 2004; Osborn 2000; Verder 2011). All three can be performed on amniotic fluid, first gastric aspirate, or tracheal aspirate soon after birth (Fiori 2004; Osborn 2000). The click test demonstrates high sensitivity (94%) and specificity (100%) utilizing tracheal aspirate in preterm infants (Skelton 1994), as well as high interobserver reliability (Osborn 1998). The stable microbubble test demonstrates lower sensitivity (57%) and specificity (96%) utilizing amniotic fluid just prior to delivery (Chida 1993). Lamellar body counts of gastric aspirates demonstrates moderate sensitivity (75%) and low specificity (72%) (Verder 2011). The lecithin‐to‐sphingomyelin (L/S) ratio and phosphatidylglycerol (PG) presence in amniotic fluid or tracheal aspirate has also been used (Merritt 1991; Verder 2017).

In addition to testing for surfactant deficiency after birth, there are many antenatal tests for fetal lung maturity. These include analysis of amniotic fluid for L/S ratio, concentration of PG, rapid agglutination testing for anti‐PG antibodies, lamellar body count, and the now‐discontinued TDx‐Fetal Lung Maturity (FLM) II assay (surfactant‐to‐albumin ratio) (Yarbrough 2014). However, FLM testing utilization has steadily decreased (McGinnis 2008). This is thought to be secondary to improved fetal outcomes with increased use of antenatal steroids (McGinnis 2008).

How the intervention might work

While there has been significant advancement in the treatment of newborns who develop RDS, there is continued need to identify sooner those that who would benefit from surfactant treatment without waiting for dramatic clinical signs of respiratory distress, as is the case with selective administration. Such an intervention would include the incorporation of rapid tests for lung maturity at the early stage of respiratory distress. However, this intervention is distinct from a conventional early administration protocol, as it considers lung maturity in addition to the need for respiratory support during the first two hours of life.

Alternatively, the rapid evaluation of lung maturity of neonates who are at high risk of developing RDS is also needed. This approach is distinct from the prophylactic surfactant administration of high‐risk infants, as it would allow for the option of not treating those who demonstrate sufficient lung maturity.

Why it is important to do this review

The administration of exogenous surfactant is not without harm. Examples include risks associated with instillation (bradycardia, hypoxemia, blockage of endotracheal tube), pulmonary hemorrhage, lung overdistension and hyperventilation (Lopez 2013). Hence there is a desire to further limit administration only to neonates who are surfactant deficient and will benefit from surfactant administration, and spare those who are not deficient from the potential side effects.

Objectives

To assess the effects of surfactant treatment guided by rapid tests for surfactant deficiency in preterm infants at risk for or having RDS.

Comparison 1: In preterm infants at risk for RDS, does surfactant treatment guided by rapid tests for surfactant deficiency compared to prophylactic surfactant administration to all high‐risk infants minimize the need for surfactant treatment and prevent bronchopulmonary dysplasia and mortality?

Comparison 2: In preterm infants who require early respiratory support, does surfactant treatment guided by rapid tests for surfactant deficiency compared to surfactant therapy provided to infants with RDS diagnosed on clinical and radiologic criteria minimize the need for surfactant treatment and prevent bronchopulmonary dysplasia and mortality?

Planned subgroup analysis: gestational age, disease severity, timing of testing and treatment, surfactant preparation, exposure to antenatal steroids.

Methods

Criteria for considering studies for this review

Types of studies

Randomized and quasi‐randomized controlled trials and cluster‐randomized controlled trials that evaluate physiochemical tests for surfactant deficiency. We will exclude cross‐over trials.

Types of participants

Participants included in Comparison 1: Prevention/prophylaxis: Preterm infants at high risk of developing RDS include extremely preterm (less than 28 weeks' gestation) and very preterm (28 to 32 weeks' gestation) irrespective of need for respiratory support.

Participants included in Comparison 2: Treatment of established disease: Preterm infants who require early respiratory support including extremely preterm (less than 28 weeks' gestation), very preterm (28 to 32 weeks' gestation), and moderate‐to‐late preterm (32 to 37 weeks' gestation). Early respiratory support would include utilization of supplemental oxygen, high flow nasal cannula, continuous positive airway pressure or assisted ventilation.

Excluded populations: Term or late preterm infants with other causes of respiratory distress including meconium aspiration syndrome, pulmonary infection, acute respiratory distress syndrome, and congenital diaphragmatic hernia (Lopez 2013). We will not include these alternate applications of exogenous surfactant therapy in our review.

Types of interventions

We will evaluate the utilization of rapid test after birth for surfactant deficiency in infants at high risk of RDS or requiring respiratory support.

Rapid tests will include the click test (Osborn 2000), lamellar body counts (Verder 2011), and stable microbubble test (Fiori 2004), as well as any less common test insomuch as the test is able to assess surfactant deficiency in a reasonable time frame to inform clinical management.

Comparison 1: Intervention: surfactant treatment guided by rapid tests for surfactant deficiency; Control: prophylactic surfactant administration to all high‐risk infants.

Comparison 2: Intervention: surfactant treatment guided by rapid tests for surfactant deficiency; Control: surfactant therapy provided to infants with RDS diagnosed on clinical and radiologic criteria.

We will include all methods of surfactant administration as well as all surfactant products utilized in the original research studies.

Types of outcome measures

Primary outcomes

  1. Neonatal mortality (mortality < 28 days of age) from any cause.

  2. Mortality prior to hospital discharge (from any cause).

  3. Bronchopulmonary dysplasia (use of supplemental oxygen at 36 weeks' postmenstrual age in infants born before 32 weeks' gestation; or use of supplemental oxygen > 28 days of age in infants born after 32 weeks' gestation).

  4. Bronchopulmonary dysplasia or mortality (use of supplemental oxygen at 36 weeks' postmenstrual age in infants born before 32 weeks' gestation; or use of supplemental oxygen > 28 days of age in infants born after 32 weeks' gestation; any‐cause mortality).

Secondary outcomes

  1. Surfactant utilization (number of infants receiving surfactant)

  2. Any air leak syndromes (including pulmonary interstitial emphysema, pneumothorax, pneumomediastinum).

  3. Any pneumothorax.

  4. Pulmonary interstitial emphysema.

  5. Any pulmonary hemorrhage.

  6. Use of supplemental oxygen at 28 to 30 days of age.

  7. Use of supplemental oxygen or death prior to 28 to 30 days of age.

  8. Patent ductus arteriosus (treated pharmacologically (cyclo‐oxygenase inhibitor, paracetamol) or surgically).

  9. Any culture‐proven bacterial sepsis.

  10. Any culture‐proven fungal sepsis.

  11. Necrotizing enterocolitis (defined as Bell stage II or greater) (Bell 1978).

  12. Intraventricular hemorrhage (any grade and severe (grade 3 to 4)) (Papile 1978).

  13. Periventricular leukomalacia.

  14. Retinopathy of prematurity (all grade and severe (stage 3 or greater)) (ICCROP 2005).

  15. Length of hospital stay (days)

  16. Cerebral palsy. (Clinical cerebral palsy diagnosed if the child had a non‐progressive motor impairment characterized by abnormal muscle tone and decreased range or control of movements. If data are available, we will determine the level of gross motor function using the Gross Motor Function Classification System (Palisano 1997)).

  17. Neurodevelopmental outcome at approximately two years' corrected age (acceptable range 18 months to 28 months) including: cerebral palsy, significant mental developmental delay (Bayley Scales of Infant Development Mental Developmental Index < 70) (Bayley 1993), legal blindness (< 20/200 visual acuity), and hearing deficit (aided or < 60 dB on audiometric testing). The composite outcome “neurodevelopmental impairment” was defined as having any one of the aforementioned deficits (modified from definitions of moderate‐to‐severe developmental delay) (Schmidt 2007).

Search methods for identification of studies

We will use the criteria and standard methods of Cochrane and Cochrane Neonatal (see the Cochrane Neonatal search strategy for specialized register). We will search for errata or retractions from included studies published in full text on PubMed (www.ncbi.nlm.nih.gov/pubmed) and report the date this was done in the review.

Electronic searches

We will conduct a comprehensive search including: Cochrane Central Register of Controlled Trials (CENTRAL, current issue) in the Cochrane Library; MEDLINE via PubMed (1996 to current); Embase (1980 to current); and CINAHL (Cumulative Index to Nursing and Allied Health Literature) (1982 to current) using the following search terms: (Pulmonary Surfactants[MeSH] OR surfactant* OR Beractant OR Poractant OR Curosurf OR Survanta OR Exosurf OR Lucinactant), plus database‐specific limiters for randomized controlled trials and neonates (see Appendix 1 for the full search strategies for each database). We will not apply language restrictions. We will search the following clinical trials registries for ongoing or recently completed trials: US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (clinicaltrials.gov), the World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) (www.who.int/ictrp/en/), and the ISRCTN registry (www.isrctn.com/).

Searching other resources

We will also review the reference lists of all identified articles for relevant articles not located in the primary search.

Data collection and analysis

We will collect information regarding the method of randomization, blinding, intervention, stratification, and whether the trial was single or multicenter for each included study. We will note information regarding trial participants including gestational age criteria, birth weight criteria, exposure to antenatal steroids, and other inclusion or exclusion criteria. We will analyze the clinical outcomes noted above in Types of outcome measures.

Selection of studies

We will include all randomized, quasi‐randomized, and cluster‐randomized controlled trials fulfilling our inclusion criteria. All review authors will review the results of the search and separately select studies for inclusion. Any disagreements will be resolved by discussion.

We will record the selection process in sufficient detail to complete a PRISMA flow diagram and 'Characteristics of excluded studies' table (Moher 2009).

Data extraction and management

Two review authors (CK and RS) will extract, assess, and code all data for each study, using a form designed specifically for this review. Any standard error of the mean will be replaced by the corresponding standard deviation. Any disagreements will be resolved by discussion. One review author will enter final data for each study into Review Manager 5 (Review Manager 2014), which the other review author (RS) will check. All review authors will review the protocol, analysis, and draft manuscript.

Assessment of risk of bias in included studies

Two review authors will independently assess the risk of bias (low, high, or unclear) of all included trials using the Cochrane ‘Risk of bias’ tool for the following domains (Higgins 2017).

  1. Sequence generation (selection bias)

  2. Allocation concealment (selection bias)

  3. Blinding of participants and personnel (performance bias)

  4. Blinding of outcome assessment (detection bias)

  5. Incomplete outcome data (attrition bias)

  6. Selective reporting (reporting bias)

  7. Any other bias

Any disagreements will be resolved by discussion or by consulting a third assessor. See Appendix 2 for a more detailed description of risk of bias for each domain.

Measures of treatment effect

We will perform the statistical analyses using Review Manager 5 software (Review Manager 2014). We will analyze categorical data using risk ratio (RR) and risk difference (RD). For statistically significant outcomes, we will calculate the number needed to treat for an additional beneficial outcome (NNTB) or number needed to treat for an additional harmful outcome (NNTH). We will calculate mean differences (MDs) between treatment groups where outcomes are measured in the same way for continuous data. Where outcomes are measured differently, we will report data as standardized mean differences (SMD). We will report 95% confidence intervals (CIs) for all outcomes.

Unit of analysis issues

The unit of analysis will be the participating infant in individually randomized trials, and an infant will be considered only once in the analysis. The participating neonatal unit or section of a neonatal unit or hospital will be the unit of analysis in cluster‐randomized trials. We will analyze them using an estimate of the intracluster correlation coefficient (ICC) derived from the trial (if possible), or from a similar trial or from a study with a similar population as described in Section 16.3.6 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017). If we use ICCs from a similar trial or from a study with a similar population, we will report this and conduct a sensitivity analysis to investigate the effect of variation in the ICC.

If we identify both cluster‐randomized trials and individually randomized trials, we will only combine the results from both if there is little heterogeneity between the study designs, and the interaction between the effect of the intervention and the choice of randomization unit is considered to be unlikely.

We will acknowledge any possible heterogeneity in the randomization unit and perform a sensitivity analysis to investigate possible effects of the randomization unit.

Dealing with missing data

Where feasible, we intend to carry out analysis on an intention‐to‐treat basis for all outcomes. Whenever possible, we will analyze all participants in the treatment group to which they were randomized, regardless of the actual treatment received. If we identify important missing data (in the outcomes) or unclear data, we will request the missing data by contacting the original investigators. We will make explicit the assumptions of any methods used to deal with missing data. We may perform sensitivity analyses to assess how sensitive results are to reasonable changes in the undertaken assumptions. We will address the potential impact of missing data on the findings of the review in the ’Discussion’ section.

Assessment of heterogeneity

We will estimate the treatment effects of individual trials and examine heterogeneity among trials by inspecting the forest plots and quantifying the impact of heterogeneity using the I² statistic. We will grade the degree of heterogeneity as: less than 25% no heterogeneity; 25% to 49% low heterogeneity; 50% to 75% moderate heterogeneity; more than 75% substantial heterogeneity. If we note statistical heterogeneity (I² > 50%), we will explore the possible causes (e.g. differences in study quality, participants, intervention regimens, or outcome assessments).

Assessment of reporting biases

We intend to conduct a comprehensive search for eligible studies and will be alert for duplication of data. If we identify 10 or more trials for meta‐analysis, we will assess possible publication bias by inspection of a funnel plot. If we uncover reporting bias that could, in the opinion of the review authors, introduce serious bias, we will conduct a sensitivity analysis to determine the effect of including and excluding these studies in the analysis.

Data synthesis

If we identify multiple studies that we consider to be sufficiently similar, we will perform meta‐analysis using Review Manager 5 (Review Manager 2014). For categorical outcomes, we will calculate the typical estimates of RR and RD, each with its 95% CI; for continuous outcomes, we will calculate the mean difference or the standardized mean difference, each with its 95% CI. We will use a fixed‐effect model to combine data where it is reasonable to assume that studies were estimating the same underlying treatment effect. If we judge meta‐analysis to be inappropriate, we will analyze and interpret individual trials separately. If there is evidence of clinical heterogeneity, we will try to explain this based on the different study characteristics and subgroup analyses.

Quality of evidence

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

  1. Neonatal mortality (mortality < 28 days of age) from any cause.

  2. Mortality prior to hospital discharge (from any cause).

  3. Bronchopulmonary dysplasia (use of supplemental oxygen at 36 weeks' postmenstrual age in infants born before 32 weeks' gestation; or use of supplemental oxygen > 28 days of age in infants born after 32 weeks' gestation).

  4. Bronchopulmonary dysplasia or mortality (use of supplemental oxygen at 36 weeks' postmenstrual age in infants born before 32 weeks' gestation; or use of supplemental oxygen > 28 days of age in infants born after 32 weeks' gestation; any‐cause mortality).

  5. Any pneumothorax.

  6. Neurodevelopmental outcome at approximately two years' corrected age (acceptable range 18 months to 28 months) including: cerebral palsy, significant mental developmental delay (Bayley Scales of Infant Development Mental Developmental Index < 70) (Bayley 1993), legal blindness (< 20/200 visual acuity), and hearing deficit (aided or < 60 dB on audiometric testing). The composite outcome “neurodevelopmental impairment” was defined as having any one of the aforementioned deficits (modified from definitions of moderate‐to‐severe developmental delay) (Schmidt 2007).

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

The GRADE approach results in an assessment of the quality of a body of evidence in one of the following four grades.

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

  2. 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.

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

  4. 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

In addition to considering the management of high‐risk infants (often prophylactic) and low‐risk infants (often selective use based on clinical reasoning), we will evaluate the role of rapid testing for surfactant deficiency in cases where mothers did or did not receive antenatal steroids or in which the child was not provided continuous positive airway pressure.

Planned subgroup analysis: gestational age (< 28 weeks' gestational age), disease severity (need for assisted ventilation, need for FiO2 > 0.4), type of rapid test, timing of testing and treatment, exposure to antenatal steroids, surfactant preparation.

Sensitivity analysis

Where we identify substantial heterogeneity, we will conduct sensitivity analysis to determine if the findings are affected by inclusion of only those trials considered to have used adequate methodology with a low risk of bias (selection and performance bias). We will report results of sensitivity analyses for primary outcomes only.

Acknowledgements

The methods section of this protocol is based on a standard template used by Cochrane Neonatal.

Appendices

Appendix 1. Cochrane Neonatal standard search strategy

PubMed: ((infant, newborn[MeSH] OR newborn OR neonate OR neonatal OR premature OR low birth weight OR VLBW OR LBW or infan* or neonat*) AND (randomized controlled trial [pt] OR controlled clinical trial [pt] OR randomized [tiab] OR placebo [tiab] OR drug therapy [sh] OR randomly [tiab] OR trial [tiab] OR groups [tiab]) NOT (animals [mh] NOT humans [mh]))

Embase: ((exp infant) OR (infan* OR newborn or neonat* OR premature or very low birth weight or low birth weight or VLBW or LBW).mp AND (human not animal) AND (randomized controlled trial or controlled clinical trial or randomized or placebo or clinical trials as topic or randomly or trial or clinical trial).mp

CINAHL: (infan* OR newborn OR neonat* OR premature OR low birth weight OR VLBW OR LBW) AND (randomized controlled trial OR controlled clinical trial OR randomized OR placebo OR clinical trials as topic OR randomly OR trial OR PT clinical trial)

Cochrane Library: (infan* or newborn or neonat* or premature or preterm or very low birth weight or low birth weight or VLBW or LBW)

Appendix 2. 'Risk of bias' tool

We will use the standard methods of Cochrane and Cochrane Neonatal to assess the methodological quality of the trials. For each trial, we will seek information regarding the method of randomization, blinding, and reporting of all outcomes of all the infants enrolled in the trial. We will assess each criterion as being at a low, high, or unclear risk of bias. Two review authors will separately assess each study. Any disagreements will be resolved by discussion. We will add this information to the 'Characteristics of included studies' table. We will evaluate the following issues and enter the findings into the 'Risk of bias' table.

1. Sequence generation (checking for possible selection bias). Was the allocation sequence adequately generated?

For each included study, we will categorize the method used to generate the allocation sequence as:

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

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

  • unclear risk.

2. Allocation concealment (checking for possible selection bias). Was allocation adequately concealed?

For each included study, we will categorize the method used to conceal the allocation sequence as:

  • low risk (e.g. telephone or central randomization; consecutively numbered, sealed, opaque envelopes);

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

  • unclear risk

3. Blinding of participants and personnel (checking for possible performance bias). Was knowledge of the allocated intervention adequately prevented during the study?

For each included study, we will categorize the methods used to blind study participants and personnel from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or class of outcomes. We will categorize the methods as:

  • low risk, high risk, or unclear risk for participants; and

  • low risk, high risk, or unclear risk for personnel.

4. Blinding of outcome assessment (checking for possible detection bias). Was knowledge of the allocated intervention adequately prevented at the time of outcome assessment?

For each included study, we will categorize the methods used to blind outcome assessment. We will assess blinding separately for different outcomes or class of outcomes. We will categorize the methods as:

  • low risk for outcome assessors;

  • high risk for outcome assessors; or

  • unclear risk for outcome assessors.

5. Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts, protocol deviations). Were incomplete outcome data adequately addressed?

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 as:

  • low risk (< 20% missing data);

  • high risk (≥ 20% missing data); or

  • unclear risk.

6. Selective reporting bias. Are reports of the study free of the suggestion of selective outcome reporting?

For each included study, we will describe how we investigated the possibility of selective outcome reporting bias and what we found. 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 methods as:

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

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

  • unclear risk.

7. Other sources of bias. Was the study apparently free of other problems that could put it at high risk of bias?

For each included study, we will describe any important concerns we had 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;

  • high risk;

  • unclear risk.

If needed, we plan to explore the impact of the level of bias by undertaking sensitivity analyses.

Contributions of authors

Colby R Kearl reviewed and drafted the protocol.

Leslie Young reviewed the protocol.

Roger Soll reviewed and helped draft the protocol.

Sources of support

Internal sources

  • No sources of support supplied

External sources

  • Vermont Oxford Network, USA.

    Vermont Oxford Network is a not‐for‐profit voluntary collaboration of Neonatal Intensive Care Units dedicated to improving newborn care throughout the world. Vermont Oxford Network supports administrative needs of Cochrane Neonatal.

  • National Institute for Health Research, UK.

    Editorial support for Cochrane Neonatal has been funded by a UK National Institute of Health Research Grant (NIHR) Cochrane Programme Grant (13/89/12). The views expressed in this publication are those of the authors and not necessarily those of the National Health Service (NHS), the NIHR, or the UK Department of Health.

Declarations of interest

Colby R Kearl has no relevant interests to declare.

Leslie Young has no relevant interests to declare.

Roger Soll is the Co‐ordinating Editor of Cochrane Neonatal (therefore the review was seen and edited by other members of the editorial team). In addition, he has previously acted as a consultant to various pharmaceutical companies that manufacture surfactant, but none in the last 10 years.

New

References

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