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. 2019 Apr 12;2019(4):CD013309. doi: 10.1002/14651858.CD013309

Continuous glucose monitoring for the prevention of morbidity and mortality in preterm infants

Alfonso Galderisi 1, Matteo Bruschettini 2,3,✉, Chiara Russo 4, Rebecka Hall 5, Daniele Trevisanuto 6
PMCID: PMC6460241

Abstract

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

To assess whether continuous glucose monitoring (CGM) versus any intermittent monitoring modalities to measure glycemia improves neurodevelopmental outcomes in preterm newborn infants.

Background

Description of the condition

Glucose homeostasis poses a significant challenge for preterm infants, and there is little evidence for what the optimal target glucose levels should be and the effect of hypoglycemia and hyperglycemia on neurodevelopmental outcome remains controversial (McKinlay 2015; McKinlay 2017; Tottman 2017). Preterm neonates are susceptible to hypoglycemia (Adamnkin 2017), as a consequence of immature gluconeogenesis and ketogenesis, and to hyperglycemia (Farrag 2000), due to impaired insulin response to glucose variations during the first days of life. Given their high brain‐to‐body mass ratio, preterm infants have almost double the requirement for glucose (6 to 8 mg/kg/min) of term neonates (2 to 3 mg/kg/day) (Hay 2009). The high oxidative activity of the brain, and consequently the high requirement of glucose and oxygen, contributes to the extreme susceptibility of neuronal tissue to hypoglycemic injury during the first weeks of life (Burns 2008; Ferriero 2016; Wong 2013). In experimental animal models, Hoiland 2016 described a direct effect of glucose on smooth muscle cells of cerebral vessels through the inhibition of K‐ATP channels. This mechanism, along with a direct cytotoxic effect of hypoglycemia, would sustain a hypothetical relationship between cerebral blood flow/cerebral oxygenation and glycemic level.

Despite the growing evidence of the effect of prolonged glucose imbalance on brain development, we still lack consistent recommendation for glucose monitoring in preterm neonates. Traditional strategies are based on point‐of‐care measures of blood glucose that provide punctual values and largely underestimate the actual prevalence of hypoglycemic events (Uettwiller 2015), and consequently the time of exposure to low blood glucose, which is the main determinant of the neuronal damage. Additionally, point‐of‐care measures by heel prick test to measure glycemic status is a painful procedure with potential long‐term adverse effects on brain development (Ranger 2013).

Subcutaneous sensors for continuous glucose monitoring (CGM) are a new area of opportunity for neonatal care. Indeed, CGM has been successfully used for diabetes management in pediatric and adult patients to drive insulin infusion in automated and semi‐automated devices that represent a major improvement in the field. Their use in neonatal care holds the potential of providing a continuous measure of subcutaneous glucose, along with the opportunity of providing alerts for hypoglycemia or hyperglycemia and driving therapeutic interventions (Harris 2013).

The accuracy of CGM is comparable to point‐of‐care blood tests, with a mean absolute relative difference with blood glucose measures below 12% in adults (Fonseca 2016), and is expected to further improve with the use of more recent devices. Despite other technical limits that may limit the sensors' performance in preterm neonates (such as the lack of age‐specific sensors and the effect of interstitial fluid composition on sensor readings) (Harris 2013), this tool remains a forefront method to monitor glucose in preterm infants, whose long‐term benefits have as yet to be fully explored.

Description of the intervention

The use of CGM is safe in term and preterm neonates (Beardsall 2008), and may represent a paradigm shift in the field of neonatal metabolic studies, offering a continuous measure of glucose values and representing a guide for interventions aimed to improve glycemic control. Real‐time CGM consists of a subcutaneous glucose sensor and a non‐implantable transmitter that powers the sensor and sends data to a remote monitor via bluetooth wireless technology (Figure 1). The stream of data provides updated measurements of subcutaneous values every five minutes and real‐time display with customizable alerts for low (hereafter referred to as hypoglycemia) or high (hereafter referred to as hyperglycemia) subcutaneous glucose values (Beardsall 2008). The current sensors may remain in place for up to 14 days without needing replacement and need twice daily calibration with blood glucose measurements. Most recent sensors have factory‐calibration and do not require additional blood glucose tests during their placement. However, the commercially available devices have been labeled by European and USA regulatory agencies for children aged two years and older, although there is a growing body of data that supports their safe use in younger population, including term and preterm neonates (Beardsall 2013; Galderisi 2018).

Figure 1.

Figure 1

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Continuous glucose monitoring: outline of the main components of the sensor

CGM sensors may provide trend information, such as the rate of glucose change, that can guide clinical choices or be integrated in computer‐based tools for individualizing the glucose intakes or insulin delivery in the presence of hypoglycemia or hyperglycemia.

Different commercial brands for CGM tools have distinctive features regarding the necessity for or not for daily calibration, the connectivity with other devices and the insertion technique. However, the sensing system is similar for the most commonly used manufacturers. Commonly used medications, such as acetaminophen, may affect the sensor performance and the necessity for their use should be evaluated in the choice of a specific sensor.

The commercially available sensors, labeled for diabetes care, can be linked to algorithms for the adjustment of insulin delivery (so called hybrid closed loop) (Galderisi 2017). However, integrated tools are not currently available for neonatal care and we can rely only on investigational devices combining, based on the individual expertise of the researcher group and the study design, commercial CGM with investigational algorithms directly connected to delivery systems or to computer‐based platforms that will operate as enhanced advisors for the neonatal intensive care unit (NICU) personnel.

CGM insertion is associated with lower pain scores compared with the heel stick (Galderisi 2018), and its use might reduce daily heel pricks necessary to monitor blood glucose during the first days of life. This represents a clinically relevant outcome as early exposure to pain is associated with a modified cerebral structure studied with diffusion magnetic resonance imaging (MRI) in specific parts of the brain (Brummelte 2012).

How the intervention might work

The effect of neonatal glycemic control on short‐term morbidity, as well as long‐term neurodevelopmental outcome, is still controversial.

As time spent in hypoglycemia or hyperglycemia is known to play a major role in determining acute brain damage in children and adults (Cryer 2007), we can hypothesize that neonatal measures of glycemic control based on CGM would be more reliable to assess the meaningfulness of such a variable, as well as to drive therapeutic interventions.

Current interventions based on CGM may adopt the sensor:

  • as an isolated monitoring tool to prompt corrective actions for both hypoglycemia and hyperglycemia. This approach is expected to increase the rate of detection of hypoglycemia and hyperglycemia, minimizing the overall time spent out of target range;

  • combined with computer‐based algorithms to adapt glucose or insulin infusion based on CGM readings;

  • combined with computer‐based algorithms to adapt glucose or insulin infusion based on alerts for hypoglycemia or hyperglycemia from CGM, after confirmatory blood glucose test.

Computer‐based algorithms suggest changes in glucose or insulin infusion based on the actual CGM with or without confirmatory blood glucose values, the trend values, and the prespecified glycemic target. Three control approaches have been used to optimize glycemic control by means of insulin delivery adjustments, based on CGM: the proportional integrative derivative (PID), the model predictive control (MPC), and the fuzzy logic controller (Steil 2013; Steil 2006). The input to a controller is usually the glucose level and the outputs can be glucose infusion rate/intakes or insulin delivery. The algorithms or models are meant to reproduce the physiological response to glycemic changes based on a priori assumptions that inform the model and are adjusted over time according to the input.

In neonatal care, differently from the diabetes care these tools were initially developed for, we may observe algorithms designed either to adjust only the glucose infusion rate or both glucose or insulin. The glycemic target (target range or fixed limit), the time in between each adjustment, and the temporary window adopted to feed the algorithm evaluation are the pillars of an algorithm‐based approach. 

CGM might be used as a stand‐alone device too, with caregivers deciding the adjustments based on their own experience or protocols. However, an algorithm‐based approach is expected to maximize the benefits deriving from the use of these devices.

Additional advantages may be associated with CGM use. Reducing the frequency of blood sampling may reduce the risk of anemia and the need for blood transfusions. Furthermore, in the absence of a central line, CGM would avoid stressful stimuli due to heel lance, in a fashion similar to what is seen with the use of continuous transcutaneous carbon dioxide monitoring (Bruschettini 2016).

Why it is important to do this review

The lack of long‐term studies on CGM means there remains a major gap in knowledge in this field. Although there are narrative reviews on the use of CGM in newborns (McKinlay 2017; Shah 2018), there is a lack of systematic reviews and meta‐analysis on the use of CGM in preterm neonates.

This is a compelling task, due to the growing number of neonatal studies adopting devices for CGM either for detecting hypoglycemia and hyperglycemia or for driving targeted therapeutical interventions (Beardsall 2008; Galderisi 2018).

In this Cochrane Review we will analyze the available evidence for short‐ and long‐term benefits deriving from CGM use in preterm infants.

Objectives

To assess whether continuous glucose monitoring (CGM) versus any intermittent monitoring modalities to measure glycemia improves neurodevelopmental outcomes in preterm newborn infants.

Methods

Criteria for considering studies for this review

Types of studies

We will include prospective randomized clinical controlled trials, quasi‐randomized controlled trials (quasi‐RCTs), and cluster‐randomized controlled trials (cluster‐RCTs). We will exclude cross‐over trials because the intervention may have a lasting effect that compromises entry to subsequent periods of the trial.

We will include published studies, unpublished studies, and studies published only as abstracts if assessment of study quality is possible and other inclusion criteria are fulfilled. 

Types of participants

We will include preterm infants (i.e. < 37 weeks' gestational age) of any birth weight, any postnatal age, admitted to NICUs or nursery.

We will include infants who have received prior treatment for hypoglycemia or hyperglycemia.

Types of interventions

We plan to include the following comparisons:

  • comparison 1: CGM with or without prespecified interventions to correct hypoglycemia (e.g. algorithms; use of automated or strictly defined criteria to perform changes in glucose infusion) or hyperglycemia (e.g. changes in parenteral nutrition: insulin administration) versus intermittent modalities to measure glycemia (e.g. capillary glucose testing; central line sampling or venipuncture) with or without prespecified interventions to correct hypoglycemia or hyperglycemia;

  • comparison 2: CGM associated with prespecified interventions to correct hypoglycemia (e.g. algorithms; use of automated or strictly defined criteria to perform changes in glucose infusion) or hyperglycemia (e.g. changes in parenteral nutrition: insulin administration) versus CGM without prespecified interventions to correct hypoglycemia or hyperglycemia.

Prespecified interventions will include any automated or semi‐automated system driven by the CGM data, as well as mathematical algorithms based on CGM data to calculate the glucose or insulin to be infused; any insulin drift based on CGM; any glucose administration (bolus, change of the infusion rate, oral, or intravenous) administered to correct hypoglycemia based on CGM data.

We will address the use of CGM associated with confirmatory glycemia in the ‘Subgroup analysis and investigation of heterogeneity' section.

The masked use of CGM (i.e. to preserve blinding) associated with intermittent blood glucose testing will be considered as intermittent blood glucose testing.

We will consider brief interruption of CGM (e.g. in case of sensor repositioning) as continuous use. Though the target glycemia range might differ between trials, within each trial the glycemia target range must be identical in the intervention and control groups.

Types of outcome measures

Primary outcomes

  • Neurodevelopmental outcome including: cerebral palsy, significant mental developmental delay (Bayley Scales of Infant Development Mental Developmental Index < ‐2SD ) (Bayley 1993; Bayley 2006), legal blindness (< 20/200 visual acuity), and hearing deficit (aided or < 60 dB on audiometric testing). The composite outcome ‘neurodevelopmental impairment' is defined as having any one of the aforementioned deficits (modified from definitions of moderate to severe developmental delay) (Schmidt 2007). We will assess the outcome assessed at 18 to 36 months and 3 to 5 years of age.

Secondary outcomes

  • Impairment of executive function (BRIEF T‐score > 65) at two years and 4.5 to 5 of corrected age (Gioia 2003);

  • impairment of communicative skills assessed by caregivers’ questionnaires (MacArthur‐Bates communicative development inventory score (MB‐CDI) at two years and 4.5 to 5 of corrected age (Fenson 2007);

  • neonatal death (first 28 days; all‐cause mortality);

  • death during initial hospitalization (all‐cause mortality);

  • seizures during neonatal period (yes/no). We will only report seizures after study entry;

  • hypoglycemia episodes (number from study entry to discontinuation of glucose monitoring; number from study entry to hospital discharge) per patient detected by CGM or masked use of CGM. Though the definition of hypoglycemic episodes (threshold and duration) might differ between trials, within each trial the definition of hypoglycemic episode must be identical in both study groups;

  • hyperglycemia episodes (number from study entry to discontinuation of glucose monitoring; number from study entry to hospital discharge) per patient detected by CGM or masked use of CGM. Though the definition of hyperglycemic episodes (threshold and duration) might differ between trials, within each trial the definition of hyperglycemic episode must be identical in both study groups;

  • requirement for any medications for hypoglycemia (from study entry to discontinuation of glucose monitoring), e.g. glucagon or corticosteroids (yes/no);

  • requirement for any medications for hyperglycemia (from study entry to discontinuation of glucose monitoring), e.g. insulin (yes/no);

  • need for blood transfusions during initial hospitalization (yes/no);

  • any germinal matrix‐intraventricular hemorrhage (IVH): any IVH, grades 1 to 4 (according to Papile classification; Papile 1978);

  • severe IVH: ultrasound diagnosis grades 3 and 4 (according to Papile classification; Papile 1978);

  • cerebellar hemorrhage on brain ultrasound in the first month of life (yes/no; Graça 2013);

  • cystic periventricular leukomalacia on brain ultrasound in the first month of life;

  • brain MRI abnormalities at term equivalent age (yes/no), defined as white matter lesions (i.e. cavitations (Rutherford 2010) and punctate lesions (Cornette 2002); germinal matrix (GM)‐IVH (Parodi 2015); or cerebellar hemorrhage (Fumagalli 2009; Limperopoulos 2007);

  • retinopathy of prematurity: any and severe (≥ stage 3; ICROP 1984);

  • bronchopulmonary dysplasia/chronic lung disease, defined as:

    • respiratory support or oxygen, or both, at 28 days of life (Ehrenkranz 2005);

    • respiratory support or oxygen, or both, at 36 weeks of postmenstrual age (PMA) (Jobe 2001);

    • physiological definition (Walsh 2004);

  • duration of initial hospital stay (days);

  • pain during CGM insertion and blood sampling for glucose monitoring, e.g. heel stick, venipuncture. We will include the following pain scales: PIPP scale (Gibbins 2014; Stevens 1996); Neonatal Pain, Agitation, and Sedation Scale (N‐PASS) (Hummel 2008; Hummel 2010); Neonatal Infant Pain Scale (NIPS) (Lawrence 1993); Neonatal Facial Coding System (NFCS) (Grunau 1998; Peters 2003); ‘Faceless’ Acute Neonatal pain Scale (FANS) (Milesi 2010); CRIES (Krechel 1995). We plan to report the mean values of each analgesia scale assessed during the procedure and at 1 to 2 hours after the procedure;

  • number of skin‐breaking procedures associated to blood glucose testing: insertion and repositioning of the CGM; intermittent modalities to measure glycemia (e.g. capillary glucose testing; venipuncture).

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 will report the date we perform this 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 (1982 to current) using the following search terms:(("Blood Glucose"[Mesh] AND "Monitoring, Physiologic"[Mesh]) OR (continuous AND glucose AND monitor*) OR CGM[tiab] OR "glucose control") AND ("Hyperglycemia"[Mesh] OR "Hypoglycemia"[Mesh] OR glycemia OR glycaemia OR "glycemic levels" OR Hypoglyc*[tiab] OR Hyperglyc*[tiab]), plus database‐specific limiters for RCTs and neonates (see Appendix 1 for the full search strategies for each database). We will not apply language restrictions. We will search clinical trials registries for ongoing or recently completed trials (ClinicalTrials.gov (clinicaltrials.gov); the World Health Organization International Clinical Trials Registry Platform (WHO ICTRP; http://apps.who.int/trialsearch/default.aspx), and the ISRCTN Registry (www.isrctn.com/)).

Searching other resources

We will assess the reference lists of all identified articles for relevant articles not identified by the primary electronic searches.

Data collection and analysis

We will use the standard methods of the Cochrane Neonatal Review Group, as described below.

Selection of studies

Two review authors (AG and CR) will independently search for and identify eligible trials that meet the inclusion criteria. We will screen the titles and abstracts to identify potentially relevant citations, and will retrieve the full texts of all potentially relevant articles; we will independently assess the eligibility of studies by filling out eligibility forms designed in accordance with the specified inclusion criteria. We will exclude studies published only in abstract form unless the final results of the trial are reported and we can ascertain all necessary information from the abstract or authors, or both. We will review studies for relevance by assessing study design, types of participants, interventions provided, and outcome measures reported. We will resolve disagreements by discussion and, if necessary, by consulting a third review author (MB). We will contact trial authors if details of primary trials are not clear. We will record the selection process in sufficient detail to complete a PRISMA flow diagram (Moher 2009), and ‘Characteristics of excluded studies' table. 

Data extraction and management

Two review authors (AG and CR) will independently extract data using a data extraction form integrated with a modified version of the Cochrane Effective Practice and Organisation of Care (EPOC) Group data collection checklist (Cochrane EPOC 2017).

We will extract the following characteristics from each included study:

  • administrative details: study author(s); published or unpublished; year of publication; year in which study was conducted; presence of vested interest; details of other relevant papers cited;

  • study details: study design; type, duration, and completeness of follow‐up (e.g. > 80%); country and location of study; informed consent; ethics approval;

  • participant details: birth weight, gestational age, number of participants;

  • intervention details: type, duration, mode of use of CGM;

  • details of outcomes as mentioned above under the ‘Types of outcome measures' section.

We will resolve disagreements by discussion. We will describe ongoing studies identified by our search, when available, detailing the primary author, research question(s), methods, and outcome measures, together with an estimate of the reporting date.

Should any queries arise, or in cases for which additional data are required, we will contact study investigators/authors for clarification. Two review authors (RH and MB) will use RevMan Web for data entry (RevMan Web).

Assessment of risk of bias in included studies

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

  • sequence generation (selection bias);

  • allocation concealment (selection bias);

  • blinding of participants and personnel (performance bias);

  • blinding of outcome assessment (detection bias);

  • incomplete outcome data (attrition bias);

  • selective reporting (reporting bias);

  • any other bias.

We will resolve any disagreements through discussion or by consulting a third review author (RH). See Appendix 2 for a more detailed description of risk of bias for each domain.

Measures of treatment effect

We will use risk ratios (RRs), risk differences (RDs), number needed to treat for an additional beneficial outcome (NNTB), or number needed to treat for an additional harmful outcome (NNTH) for categorical variables, and mean differences (MDs) for continuous variables. We will calculate standardized MDs when combining different pain scales. We plan to replace any within‐group standard error of the mean (SEM) reported in a trial by its corresponding standard deviation (SD) using the formula SD = SEM x √N. We will report 95% confidence intervals (CIs) for each statistic. 

Unit of analysis issues

We plan to include all RCTs and quasi‐RCTs in which the unit of allocation was the individual infant. If we find any cluster‐RCTs, we will adjust analysis for the designed effect using the method stated in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017).

Dealing with missing data

We will obtain a dropout rate for each study. If we find a significant dropout rate (e.g. > 20%), we will contact study author(s) to request additional data. We will perform a sensitivity analysis to evaluate the overall results with and without inclusion of studies with a significant dropout rate. If a study reports outcomes only for participants completing the trial or only for participants who followed the protocol, we will contact study author(s) to ask them to provide additional information to facilitate an intention‐to‐treat analysis; in instances when this is not possible, we will perform a complete‐case analysis. We will address the potential impact of missing data on the findings of the review in the ‘Discussion' section.

Assessment of heterogeneity

We plan to assess clinical heterogeneity by comparing the distribution of important participant factors between trials and trial factors (randomization concealment, blinding of outcome assessment, loss to follow‐up, treatment type, co‐interventions). We will assess statistical heterogeneity by examining the I2 statistic (Higgins 2017), a quantity that describes the proportion of variation in point estimates that is due to variability across studies rather than to sampling error.

We will interpret the I2 statistic as follows:

  • < 25%: no (none) heterogeneity;

  • 25% to 49%: low heterogeneity;

  • 50% to 74%: moderate heterogeneity;

  • ≥ 75%: high heterogeneity.

In addition, we will employ the Chi2 test of homogeneity to determine the strength of evidence that heterogeneity is genuine. We will explore clinical variation across studies by comparing the distribution of important participant factors among trials and trial factors (randomization concealment, blinding of outcome assessment, loss to follow‐up, treatment types, and co‐interventions). We will consider a threshold of P value < 0.1 as an indicator of whether heterogeneity (genuine variation in effect sizes) is present.

Assessment of reporting biases

We will examine the possibility of within‐study selective outcome reporting for each study included in the review. We will search for trial protocols of included trials on electronic sources such as PubMed, ClinicalTrials.gov, and the WHO ICTRP in order to assess whether outcome reporting seem to be sufficiently complete and transparent. We will investigate publication by using funnel plots if we include 10 or more clinical trials in the systematic review (Egger 1997; Higgins 2017).

Data synthesis

We will perform statistical analyses according to the recommendations of the Cochrane Neonatal Review Group (neonatal.cochrane.org/en/index.html), and will use RevMan Web (RevMan Web). We will analyze all infants randomized on an intention‐to‐treat basis. We will analyze treatment effects in the individual trials. We will use a fixed‐effect model to combine the data. For any meta‐analyses, we will synthesize data using RR, RD, NNTT, NNTH, MD, and 95% confidence intervals (CI). We plan to analyze and interpret individual trials separately when we judge meta‐analysis to be inappropriate. 

Quality of the evidence

We will use the GRADE approach, as outlined in the GRADE Handbook (Schünemann 2013), to assess the quality of the evidence for the following (clinically relevant) outcomes: cerebral palsy, significant mental developmental delay (Bayley Scales of Infant Development Mental Developmental Index < 2 SDs), legal blindness (< 20/200 visual acuity), hearing deficit, the composite outcome ‘neurodevelopmental impairment' (defined as having any one of the four aforementioned deficits), death during initial hospitalization, and neonatal seizures.

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 but will downgrade the quality of the evidence by 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 Guideline Development Tool (GDT) to create a ‘Summary of findings’ table to report the quality of the evidence (GRADEpro GDT 2015).

The GRADE approach results in an assessment of the quality of a body of evidence and allocation to one of four grades:

  • high: we are very confident that the true effect lies close to that of the estimate of the effect;

  • moderate: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different;

  • low: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect;

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

Subgroup analysis and investigation of heterogeneity

We will present data from the following subgroups for both for hypoglycemia and hyperglycemia:

  • gestational age: ≤ 32 weeks;  > 32 weeks;

  • birth weight: < 1500 g; ≥ 1500 g;

  • use of CGM associated with intermittent modalities to measure glycemia versus CGM without intermittent modalities to measure glycemia;

  • prevention or treatment of hypoglycemia and hyperglycemia: CGM used to prevent hypoglycemia/hyperglycemia with adjustment preceding the designated threshold values or CGM used to alert for actual hypoglycemia/hyperglycemia;

  • glucose levels: euglycemic, hypoglycemic, and hyperglycemic infants;

  • control algorithm (MPC, PID, or fuzzy logic);

  • CGM coupled to a control algorithm or as a standalone device.

Sensitivity analysis

We will conduct sensitivity analyses to explore the effect of the methodological quality of trials, checking to ascertain whether studies with a high risk of bias will overestimate the effect of treatment. Differences in study design of included trials might affect the results of the systematic review. We plan to perform a sensitivity analysis to compare the effects of CGM in randomized trials as opposed to quasi‐randomized trials.

Acknowledgements

We have based the Methods section of this protocol on a standard template used by Cochrane Neonatal.

We thank Colleen Ovelman, Managing Editor, and Roger Soll, Coordinating Editor, for editorial support.

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 included 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 either low, high, or unclear risk of bias. Two review authors will separately assess each study. We will resolve any disagreement 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. Blinding will be assessed 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. Blinding will be assessed 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 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. We will search study protocols of the included trials in ClinicalTrials.gov (clinicaltrials.gov); the World Health Organization International Clinical Trials Registry Platform (WHO ICTRP; http://apps.who.int/trialsearch/default.aspx), and the ISRCTN Registry (www.isrctn.com/). 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; 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 a high risk of bias?

For each included study, we will describe any important concerns we had about other possible sources of bias (for example, 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 through sensitivity analyses.

Contributions of authors

AG and MB reviewed the background literature and wrote the protocol.

CR, RH, and DT commented on and reviewed the protocol.

All authors read and approved the final protocol version.

Sources of support

Internal sources

  • Institute for Clinical Sciences, Lund University, Lund, Sweden.

    MB is employed by this organization

External sources

  • Vermont Oxford Network, USA.

    Cochrane Neonatal Reviews are produced with support from Vermont Oxford Network, a worldwide collaboration of health professionals dedicated to providing evidence‐based care of the highest quality for newborn infants and their families.

Declarations of interest

As two review authors (AG and DT) are also the authors of one of the trials that might be included, two review authors (CR and MB) will conduct quality assessments of these trials.

New

References

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