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The Cochrane Database of Systematic Reviews logoLink to The Cochrane Database of Systematic Reviews
. 2021 Feb 12;2021(2):CD013809. doi: 10.1002/14651858.CD013809.pub2

Preoperative fasting for prevention of perioperative complications in children

Yvgeniy Oparin 1, Dena Zeraatkar 2, Harsha Shanthanna 1, Shahrzad Motaghi 2, Rachel Couban 1, Deepa Kattail 1, James Paul 1, Lawrence Mbuagbaw 2,3, Behnam Sadeghirad 1,2,✉
Editor: Cochrane Anaesthesia Group
PMCID: PMC8078500

Objectives

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

The objective of this review is to assess the effects of various preoperative fasting regimens (i.e. the duration of fasting from liquids and solids and the type and volume of permitted intake) on perioperative complications, including aspiration, aspiration‐related morbidity (e.g. aspiration pneumonia), and mortality in children undergoing general anaesthesia. We will also assess the effect of preoperative fasting regimens on other perioperative outcomes and complications, including length of hospital stay, risk of unplanned intubation and intensive care unit (ICU) admission, risk of unplanned oxygen administration, risk of unplanned admission, thirst, hunger, pain, risk of vomiting, and anxiety.

We will also use subgroup analyses to assess whether the risk of perioperative complications with various preoperative fasting regimens differ for children with a comorbidity (e.g. obesity, diabetes, respiratory, or digestive) or for children of different ages (e.g. infants, children, adolescents).

Background

Description of the condition

When general anaesthesia is induced, there is depression of the gag, cough, and swallowing reflexes (Brady 2003). These reflexes protect the airway; their reduced function during anaesthesia may lead to pulmonary aspiration should regurgitation or vomiting of gastric contents occur. This can lead to pneumonia or death (Warner 1993). This issue is of particular concern in paediatric populations, especially in younger ages, because of the need for frequent feeds with breast milk or formula to avoid hunger and dehydration. The incidence of perioperative aspiration in paediatric patients undergoing general anaesthesia has been reported as between 2 to 10 in 10,000 anaesthetics (Walker 2013; Habre 2017). Meanwhile, the incidence of serious adverse events — such as prolonged intubation — is rare, and has been reported as low as 0.4 in 10,000 anaesthetics (Walker 2013).

Description of the intervention

To reduce the risk of vomiting, regurgitation, and aspiration, the American Society of Anesthesiologists (ASA) and the European Society of Anaesthesiology (ESA) recommend a two‐hour fast from clear liquids, four‐hour fast from breast milk, six‐hour fast from infant formula, and a six‐ to eight‐hour fast from solids prior to anaesthesia (Smith 2011; ASA Committee 2017). However, in light of recent evidence, both the Canadian Anesthesiologists' Society (CAS) and the European Society for Paediatric Anaesthesiology (ESPA) have amended their guidelines to allow consumption of clear liquids up to one hour preoperatively for infants and children (Thomas 2018; Dobson 2020). Some individual centres even have policies allowing intake of clear liquids up until being called to the operating room (Andersson 2015).

Although gastric emptying may vary with age, many of the national associations, including the ASA, do not incorporate the age of the patient into their preoperative fasting guidelines (ASA Committee 2017). The Australian and New Zealand College of Anaesthetists (ANZCA) are one of the associations that do vary their guidelines with age. The ANZCA recommends: clear liquids up to two hours preoperatively for all ages; breast milk up to three hours preoperatively and formula up to four hours preoperatively for infants aged less then six months; and breast milk, formula, and limited solid foods up to six hours preoperatively for patients over six months of age (ANZCA 2017).

Prolonged preoperative fasting may cause children and infants discomfort due to thirst and hunger, anxiety, irritability, and low blood glucose (Brown 2014; ASA Committee 2017), and may increase the risk for preoperative and postoperative complications (Brown 2014). Further, different types of liquids and foods may vary in their rate of gastric emptying (Hellstrom 2006). For example, breast milk is more easily absorbed and emptied from the stomach than infant formula (Billeaud 1990). However, there is no known volume of gastric content that definitively prevents aspiration in paediatric patients undergoing general anaesthesia (Bouvet 2018).

How the intervention might work

Fasting before general anaesthesia aims to reduce the volume and acidity of stomach contents during surgery, thus reducing the risk of regurgitation or aspiration (Smith 2011; ASA Committee 2017). Medical and nursing staff concerned for their paediatric patients’ comfort and safety strive to establish safe levels of preoperative fasting without unnecessary starvation. The optimal preoperative fasting regimen, including the duration of fasting from liquids and solids and the type and volume of permitted intake, will balance the risk of aspiration or regurgitation with patient discomfort and potential adverse effects on patient recovery.

Why it is important to do this review

Despite existing guidelines, excessive fasting in children is still very common at many institutions (Engelhardt 2001; Williams 2014; Brunet‐Wood 2016; Frykholm 2018; Toms 2019). A long preoperative fasting period may cause discomfort and may compromise postoperative recovery (Brown 2014; Frykholm 2018). Another major issue is dehydration, which can make it more difficult to insert intravenous lines (which is already challenging in babies and children). For young infants, prolonged fasting may also lead to the inadequate provision of nutrition, hypoglycaemia, and ketoacidosis (Dennhardt 2015). Further, since preoperative fasting practices were initially instituted, there have been significant improvements in perioperative care and monitoring. Current evidence suggests that the risk of morbidity and mortality due to aspiration or regurgitation may be low, even with more permissive fasting regimens, and so prolonged and restrictive fasting practices may be unnecessary (Fasting 2002; Brown 2014; Thomas 2017).

Given the uncertain benefits and harms associated with various preoperative fasting regimens, and given variations in preoperative fasting practices, an up‐to‐date synthesis and appraisal of the evidence is warranted. This review will update the previous Cochrane Review addressing this topic (Brady 2009).

Objectives

The objective of this review is to assess the effects of various preoperative fasting regimens (i.e. the duration of fasting from liquids and solids and the type and volume of permitted intake) on perioperative complications, including aspiration, aspiration‐related morbidity (e.g. aspiration pneumonia), and mortality in children undergoing general anaesthesia. We will also assess the effect of preoperative fasting regimens on other perioperative outcomes and complications, including length of hospital stay, risk of unplanned intubation and intensive care unit (ICU) admission, risk of unplanned oxygen administration, risk of unplanned admission, thirst, hunger, pain, risk of vomiting, and anxiety.

We will also use subgroup analyses to assess whether the risk of perioperative complications with various preoperative fasting regimens differ for children with a comorbidity (e.g. obesity, diabetes, respiratory, or digestive) or for children of different ages (e.g. infants, children, adolescents).

Methods

Criteria for considering studies for this review

Types of studies

We will include randomized controlled trials (RCTs) and cluster‐RCTs in which children are randomized to different fasting regimens prior to undergoing general anaesthesia. We will include studies irrespective of publication status and language of publication. We will exclude all cross‐over trials because the nature of this question does not allow for cross‐over designs. We will also exclude quasi‐randomized trials, in which the assignment of participants to alternative interventions is not entirely random. 

Types of participants

We will include studies that recruited male or female patients aged less than 18 years old, who were undergoing general anaesthesia for elective or emergency surgery, including outpatient and inpatient settings. We will include studies that recruited infants, children, and adolescents but we will exclude studies that recruited neonates (aged four weeks or less). We will include children regardless of whether they suffer from any comorbidities. For trials that include only a subset of participants who are eligible, we will extract relevant data from the subset when stratified results are presented, or we will contact the trial investigators for data when stratified results are not presented. We will exclude trials if more than 20% of the participants are ineligible and data for the eligible subset cannot be obtained either from the trial report or from the trial investigators.

Types of interventions

We will include trials that compare the effects of different preoperative fasting regimens. We will group interventions according to the duration of fasting from liquids or solids; the volume of permitted intake; or the types of permitted liquids and solids. We will make comparisons within these categories (i.e. short versus longer fast from liquids; short versus longer fast from solids; fast from solids only versus fast from solids and liquids; fast from heavy or rich meals versus fast from all foods). Although their use is uncommon in children, we will include trials that administered prokinetics, H2 receptor antagonists, antacid agents, or other cointerventions, only if they were administered in both the intervention and control arms of the trial.

Types of outcome measures

Outcome measures of interest will include measures of morbidity, mortality, and patient‐reported symptoms associated with fasting. We will exclude studies that did not measure any of the critical or important outcomes listed below.

Primary outcomes
Critical outcomes

  1. Risk of aspiration‐related perioperative complications during or immediately following anaesthesia

  2. Risk of aspiration pneumonia closest to 28 days of surgery

  3. Risk of aspiration‐related mortality during or after surgery until hospital discharge

  4. Risk of all‐cause mortality during or after surgery until hospital discharge

Secondary outcomes
Important outcomes

  1. Duration of hospital stay (in days)

  2. Risk of unplanned postoperative intubation or postoperative ICU admission after surgery until hospital discharge

  3. Risk of unplanned postoperative oxygen administration during the first 24 hours after surgery

  4. Risk of unplanned postoperative hospital admission closest to 28 days of surgery

  5. Thirst prior to the administration of anaesthesia, measured by any validated binary, categorical, or continuous instrument, including visual analogue scales or number rating scales

  6. Hunger prior to the administration of anaesthesia, measured by any validated binary, categorical, or continuous instrument, including visual analogue scales or number rating scales

  7. Pain prior to the administration of anaesthesia, measured by any validated binary, categorical, or continuous instrument, including visual analogue scales or number rating scales

  8. Risk of vomiting prior to or following the administration of anaesthesia

  9. Anxiety prior to the administration of anaesthesia, measured by any validated binary, categorical, or continuous instrument, including visual analogue scales or number rating scales

Other secondary outcomes

  1. Risk of metabolic decompensation (including failure to feed, lethargy, coma, seizures, acid‐base disorders, or rhabdomyolysis) during preoperative fasting or during the first 24 hours after surgery

  2. Risk of hypoglycaemia during preoperative fasting or during the first 24 hours after surgery

  3. Risk of ketosis during preoperative fasting or during the first 24 hours after surgery

Search methods for identification of studies

Electronic searches

We will search for studies using guidelines published in the Cochrane Handbook of Systematic Reviews of Interventions in order to maximise the sensitivity of search (Higgins 2020). In the previous Cochrane Review on this topic, MEDLINE, Embase, CINAHL, and the Cochrane Central Register of Controlled Trials CENTRAL) were searched from inception to June 2009, with no restrictions on language of publication. We will update all database searches from the previous version of this review (Brady 2009). We will additionally search Web of Science from inception, with no restrictions on the language of publication or publication status. Our search strategy is available online.

Searching other resources

We will search the bibliographic references and citations of relevant studies and systematic reviews for additional potentially relevant studies. We will search the following trial registries for unpublished and ongoing studies.

We will solicit experts in the field for unpublished studies or additional eligible studies that may have been missed by our searches of electronic databases. 

Data collection and analysis

Selection of studies

At least two review authors, working independently, will screen titles and abstracts. We will retrieve full texts of articles deemed potentially eligible by at least one review author at this stage. At least two review authors, working independently, will subsequently screen the full‐text reports. Discrepancies will be resolved by discussion or third‐party adjudication. We will include a PRISMA flowchart to illustrate the screening process and we will compile a list of excluded studies with reasons why each study was excluded (Moher 2009).

Data extraction and management

We will develop and pilot a data extraction form to collect the following information from each study.

Study characteristics

  • Author

  • Year of publication

  • Study design

  • Number of participants

  • Sources of funding

  • Intraclass correlation for cluster‐randomized trials

  • Randomization and allocation procedures

  • Blinding status

  • Missing outcome data

  • Methods for measurement of outcomes

  • Prespecification of outcomes and time points in protocols or statistical analysis plans (or both)

Participant characteristics

  • Age

  • Sex

  • Weight

  • ASA status

  • Nature of surgery (i.e. elective or emergency)

  • Type of surgery (i.e. laparoscopic or non‐laparoscopic; gastrointestinal, thoracic, orthopaedic, or neurologic)

  • Comorbidities (i.e. obesity, diabetes, and gastric or respiratory disorders or diseases)

Characteristics of intervention and comparisons:

  • Details of preoperative fasting regimens in the intervention and comparison arms (e.g. duration of fasting, type of preoperative fasting (from liquids or solids), the volume of permitted intake, or the types of permitted liquids and solids)

  • Cointervention (intake of prokinetics, H2 receptor antagonists, antacid agents, or other relevant cointerventions, although these may not be routinely used in children)

Outcomes

  • Dichotomous outcomes: number of events and number of participants analysed or relative effects and confidence intervals

  • Continuous outcomes: means and standard deviations, mean differences and confidence intervals, or other measures of central tendency and variance

We will re‐extract data from trials included in the previous version of this review. If a study reports results for more than one type of analysis, we will select the analysis for extraction according to the following order of preference: 1) intention‐to‐treat analyses without any imputation for missing data; 2) intention‐to‐treat analyses with imputation; 3) per‐protocol analyses without imputation; and 4) per‐protocol analyses with imputation. A draft of our data extraction form in Microsoft Excel format is available online.

To ensure consistency in data extraction, all review authors will complete calibration exercises, which will require them to extract data from three sample trials and review and discuss discrepancies as a group. Following calibration exercises, pairs of review authors, will extract data from each study independently. Discrepancies will be resolved by discussion or third‐party adjudication.

Assessment of risk of bias in included studies

At least two review authors, working independently and in duplicate, will assess risk of bias for the effect of assignment to the intervention (i.e. the intention‐to‐treat effect) for the seven most patient‐important outcomes that will be included in the 'Summary of findings' tables (i.e. aspiration or regurgitation morbidity; all‐cause mortality; duration of hospital stay; thirst; hunger; and vomiting at the specified time points; see Types of outcome measures). We will use version 2 of the Cochrane 'Risk of bias' tool (RoB 2) (Higgins 2020, Sterne 2019), which addresses bias according to the following domains.

  • Bias from the randomization process

  • Bias due to deviations from the intended interventions

  • Bias due to missing outcome data

  • Bias in measurement of the outcome

  • Bias in selection of the reported results

Each domain will be rated as 'low risk of bias', 'some concerns' or 'high risk of bias'. We will consider studies to be at low risk of bias overall if all domains are at low risk of bias; as having some concerns overall if all domains are judged as being at low risk of bias or causing some concerns; and high risk of bias overall if one or more domains are judged to be at high risk of bias. We will use the suggested modifications to RoB 2 for assessing risk of bias in cluster‐randomized trials, adding an additional domain specific to cluster‐RCTs (bias arising from the timing of identification and recruitment of participants and bias arising from the randomization process) and we will use the signalling questions from the archived version of RoB 2.0.

We will use a macro‐enabled Microsoft Excel tool for 'Risk of bias' assessments (available from: www.riskofbias.info/welcome/rob-2-0-tool/current-version-of-rob-2) and will use the robvis tool (available from mcguinlu.shinyapps.io/robvis) to present summaries of the 'Risk of bias' assessments. We will present the details of our judgements at both the domain‐level and the overall level as supplements in the final report of the review. Review authors will resolve discrepancies by discussion or third‐party adjudication. We will not restrict our eligibility criteria based on risk of bias.

Measures of treatment effect

For dichotomous and continuous outcomes, we will calculate risk ratios and mean differences, respectively, and the corresponding standard errors. For studies that present results as medians and interquartile ranges, we will note whether outcomes are reported to be normally distributed and will impute means and standard errors using the methods described by Hozo and colleagues (Hozo 2005). We will conduct a sensitivity analysis excluding trials for which means or standard errors were imputed.

For continuous outcomes, when studies report effect estimates using different measurement scales, we will first transform all outcomes to a common instrument on a domain‐by‐domain basis, using the methods described by Thorlund and colleagues (Thorlund 2011). Briefly, this method involves rescaling instruments to the units of the most familiar instrument using linear algebra.

For continuous outcomes, we will present the minimally important difference (MID) for all pooled effect estimates. When multiple MID estimates are available for an outcome, we will use the smallest difference that has been validated.

Unit of analysis issues

We will include both individual and cluster‐RCTs, if available. For cluster‐RCTs, we will extract results from analyses that consider the cluster as the unit of randomization. For cluster‐RCTs that do not report appropriate analyses, we will contact trial investigators for the intraclass correlation coefficient and adjust results using the method presented by Rao and Scott (Rao 1992). When an intraclass correlation coefficient cannot be obtained, we will use an approximate intraclass correlation coefficient from a similar trial. The nature of this question does not allow for cross‐over designs, so we do not anticipate identifying any eligible cross‐over trials.

For trials with more than two eligible arms for inclusion in an analysis, we will either combine similar arms of the trial or include multiple effect estimates corresponding to different comparisons and split the comparator group of interest. For trials in which only select arms are eligible, we will only analyse results from comparisons of eligible arms.

Dealing with missing data

In case of missing information necessary for meta‐analysis (e.g. mean, a measure of variance, number of events, or the number of patients analysed), we will contact investigators to obtain the missing information.

We will also contact investigators in order to obtain missing outcome data. For the critical outcomes, when we are unable to retrieve missing outcome data, we will explore the impact of this by conducting sensitivity analyses that exclude studies in which the proportion of missing outcome data exceeds 10%. We will also explore the impact of missing outcome data by allowing for informative missingness in aggregate data using the METAMISS2 module in Stata (Chaimani 2018; Mavridis 2020). In this approach, we will use different models to quantify the degree of departure from the missing data at random assumption. In brief, these models relate the mean outcome in the missing data to the mean of the observed data for each trial arm through an informative missingness parameter. For continuous outcomes, we will use the informative missingness difference of means (Mavridis 2015), and for binary outcomes, we will use the informative missingness odds ratio (White 2008) as informative missingness parameters.

Assessment of heterogeneity

We will use qualitative assessment of forest plots, the Chi2 test for heterogeneity, and the I2 statistic to assess the magnitude of heterogeneity. We will consider an I2 statistic between 0% and 40% as potentially not important, 30% to 60% as moderate, 50% to 90% as substantial, and 75% to 100% as considerable heterogeneity (Higgins 2020).

Assessment of reporting biases

For analyses with 10 or more studies, we will explore non‐reporting biases (publication bias) using contour‐enhanced funnel plots using the 'confunnel' command in Stata (Peters 2008) and by conducting Harbord’s test for dichotomous outcomes and Egger’s test for continuous outcomes (Egger 1997; Harbord 2006; Harbord 2009).

Data synthesis

To account for expected variation in effects across studies, we will use the DerSimonian–Laird random‐effects model for meta‐analysis of all outcomes. We will conduct meta‐analyses using the 'metan' command and test for subgroup effects using univariate random‐effects meta‐regression in Stata (Stata). For dichotomous outcomes, we will use the number of participants in each trial arm and the number of events; for continuous outcomes, we will use means and standard deviations for each trial arm. When outcomes cannot be pooled (due to methodological issues or number of studies reporting an outcome), we will present results narratively.

Subgroup analysis and investigation of heterogeneity

We will perform the following subgroup analyses, regardless of the magnitude of observed statistical heterogeneity.

  • Age (infants aged one to 12 months versus children aged one to five years versus children older than five years)

  • Emergency versus elective surgery

  • Patients with versus those without comorbidities (i.e. obesity, diabetes, respiratory comorbidities)

  • Outpatients versus hospitalised patients

  • Risk of bias (studies at overall low risk of bias versus studies with some concerns or high risk of bias)

For primary outcomes with seven or more eligible studies, we will test for subgroup effects using the Chi2 test for interaction and we will perform random‐effects meta‐regression with modification to the variance of the estimated coefficients suggested by Knapp and Hartung (Knapp 2003).

Sensitivity analysis

We will conduct sensitivity analysis to assess the impact of missing outcome data on our results, using the methods described in Dealing with missing data.

Summary of findings and assessment of the certainty of the evidence

To summarise review findings, we will use Gradepro GDT (GRADEpro GDT) to construct separate ‘Summary of findings’ tables for comparisons involving the duration of fasting from liquids, duration of fasting from solids, the volume of permitted intake, and the types of permitted foods and drinks.

The 'Summary of findings' table will include the relative and absolute effects and the certainty of evidence for the following seven most patient‐important outcomes: aspiration‐related perioperative complications; aspiration‐related mortality; all‐cause mortality; duration of hospital stay; thirst; hunger; and vomiting. We will justify all decisions to downgrade the certainty of the evidence using footnotes and we will make additional comments to aid the reader's understanding of the review where necessary. At least two review authors, working independently, will apply the GRADE criteria to evaluate the certainty of evidence for these seven outcomes (Guyatt 2011). Evidence from randomized trials will start as high‐certainty but may be rated down due to risk of bias, imprecision, inconsistency, indirectness, and publication bias. Discrepancies will be resolved by discussion or third‐party adjudication. In case of credible subgroup effects based on characteristics of the population (i.e. baseline risk, emergency versus elective procedure, comorbidities), we will present results stratified across subgroups in the 'Summary of findings' tables.

What's new

Date Event Description
27 January 2021 New citation required but no major changes Author order and affiliations changed and minor edits made to the text.
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History

Protocol first published: Issue 1, 2021

Acknowledgements

We would like to thank Michael Heesen (Content Editor), Nathan Pace (Statistical Editor), Nicola Disma and Stephanie Bew (Peer Reviewers), the Cochrane Editorial and Methods Department ‐ Methods Support Unit, Janne Vendt (Information Specialist), Teo Quay (Managing Editor), Anupa Shah (Managing Editor, Cochrane Eyes and Vision) and Vernon Hedge (Managing Editor) and Andrew Smith (Co‐ordinating Editor) for their help and editorial advice during the preparation of this systematic review protocol.

Contributions of authors

BS, YO, and DZ contributed to study design and conception of the protocol. YO and RC handled the co‐ordination of the protocol. YO, BS, and DZ drafted the initial version of the manuscript. RC and BS drafted the search strategy. All authors critically revised the draft and approved the final manuscript as submitted and agree to be accountable for all aspects of the work.

Sources of support

Internal sources

  • None, Canada

    No funding

External sources

  • None, Canada

    No funding

Declarations of interest

Yvgeniy Oparin: none known
Dena Zeraatkar: none known
Harsha Shanthanna: none known
Shahrzad Motaghi: none known
Rachel Couban: none known
Deepa Kattail: none known
James Paul: none known
Lawrence Mbuagbaw: none known
Behnam Sadeghirad: none known

Edited (no change to conclusions)

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