What is gastric residual volume

We included randomized controlled trials (RCTs) and randomized cross‐over trials (data from the first period, i.e. before crossover only). For updates, we will also consider cluster‐RCTs if the following characteristics are known and reported: the number of clusters or the mean size of each cluster, outcome data for the total number of individuals, and an estimate of intracluster (or intraclass) correlation coefficient (ICC).

We included adults (ages 18 years or older) receiving EN via a nasogastric tube or a gastrostomy tube, with no restrictions on the type of clinical diagnoses or settings (e.g. ICU, hospital outpatients). We excluded studies involving EN feeding via tubes placed beyond the pylorus (postpyloric feeding).

We included trials assessing the following treatment regimens, for which intervention group was defined as any type of GRV monitoring during EN:

• regimens that monitored GRV at different intervals (since GRV during EN may be influenced by monitoring frequency);

• regimens that included the upper limit/threshold of GRV before intervention;

• regimens that involved a strategy for handling aspirated residual gastric fluid, such as returning it to the stomach or discarding it.

We included all methods of GRV monitoring (i.e. by aspiration/drainage from a nasogastric or a gastrostomy tube, by ultrasound exam, or by computed tomography (CT) scan). If a study used different methods of measuring GRV for different interventions, we excluded that study from this review. We defined a minimum intervention period of 24 hours and a maximum of 14 days. It was expected that the dose of EN that did not cause complications during the acute stage would be approximately seven days and that the observation period of 14 days would be considered appropriate when administering EN in the chronic phase.

We considered the following comparisons:

• more frequent (less than eight hours) versus less frequent (eight hours or greater) monitoring of GRV (Williams 2014);

• frequent (12 hours or less) versus no monitoring (Ozen 2016);

• higher GRV threshold (500 mL per six hours or greater) versus the lower threshold (less than 500 mL per six hours) at the time of aspiration (Reintam Blaser 2017);

• returning versus discarding the aspirated/drained GRV;

• protocol‐based nutrition strategy with GRV‐relevant criteria versus protocol‐based EN strategy without GRV‐related criteria or non‐protocol‐based nutrition strategy.

For this review, we defined a protocol‐based nutrition strategy with GRV‐relevant criteria as a regimen where the attending physicians were required to monitor the GRV for increasing/decreasing the EN volume. For protocol‐based EN strategy without GRV‐related criteria or any non‐protocol‐based nutrition strategies, such physician‐led monitoring of GRV was not implemented.

We conducted a comprehensive search to identify all eligible studies. We placed no restrictions on the language of publication. We translated non‐English language papers and assessed the full texts for potential inclusion in the review where necessary. We included studies available as abstracts only as well as unpublished data.

We screened the following electronic databases on 3 May 2021 based on systematic search strategies illustrated in Appendix 1, Appendix 2, Appendix 3, and Appendix 4:

• Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library (via Ovid Evidence‐Based Medicine Reviews Database (EBMR), from inception);

• MEDLINE (via Ovid from 1946);

• Embase (via Ovid from 1974);

• CINAHL (Cumulative Index to Nursing and Allied Health Literature) (via EBSCO from 1982).

We screened the reference lists of all primary studies and relevant review articles for additional information. We contacted authors of identified trials as well as experts in the field to locate other published or unpublished studies. 

For grey literature, we searched the following resources:

We also searched for errata or retractions of eligible trials on PubMed (www.ncbi.nlm.nih.gov/pubmed), and reported the date this was done in the review.

We conducted a search of clinical trial registers/trial result registers:

Two review authors (NK, RY) independently screened the titles and abstracts of all studies identified via the electronic searches and coded them as 'retrieve' (eligible, potentially eligible, or unclear) or 'do not retrieve.' We retrieved the full‐text reports of the former, and two review authors (NK, RY) independently screened these and identified studies for inclusion as well as record reasons for excluding ineligible studies. We resolved any disagreements through discussion by consulting a third review author (SA). We removed duplicate records and collated multiple reports of the same study, so that each study, rather than each report, was the unit of interest. Our study selection process is illustrated as a PRISMA flow diagram. Further study‐level information is provided in the Characteristics of included studies; Characteristics of excluded studies; Characteristics of studies awaiting classification; and Characteristics of ongoing studies tables.

For extraction of study characteristics and outcome data, we used a prestandardized data collection form that had been piloted on at least one study in the review. One review author (HY) extracted the following study characteristics from the included studies.

• Methods: study design, total duration of the study and run‐in period, number and locations of study centers, study setting, withdrawals, and date of study.

• Participants: number, mean age, age range, sex, severity of condition, diagnostic criteria, baseline lung function, smoking history, inclusion criteria, and exclusion criteria.

• Interventions: intervention method, comparison method, concomitant medications, and excluded medications.

• Outcomes: specified and collected primary and secondary outcomes, and time points reported.

• Notes: funding details for the trial and notable conflicts of interest of trial authors.

Two review authors (RY, SA) independently extracted outcome data from the included studies. In the Characteristics of included studies table, we recorded situations where outcome data were reported in an unusable manner. We resolved any disagreements by consensus or by involving a third review author (NK). One review author (HY) copied the data from the data collection form into Review Manager 5 (Review Manager 2014). We double‐checked that data had been entered correctly by comparing the study reports with the presentation of data in the systematic review. A second review author (RY or SA) spot‐checked study characteristics for accuracy against the trial report.

Two review authors (NK, RY) independently assessed risk of bias in each included study using Cochrane's risk of bias tool outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017). We resolved any disagreements by discussion or by involving a third review author (HY). As per the Cochrane risk of bias tool, we assessed risk of bias according to the following domains:

• random sequence generation;

• allocation concealment;

• blinding of participants and personnel;

• blinding of outcome assessment;

• incomplete outcome data;

• selective outcome reporting;

• other bias.

We judged each potential source of bias as high, low, or unclear, and provide a quote from the study report and justification for our judgment in the Characteristics of included studies table. We summarized our judgments for each included study in a risk of bias graph and risk of bias summary. We considered blinding separately for different key outcomes where necessary, for example, risk of bias for unblinded outcome assessment might be very different for all‐cause mortality than for a patient‐reported pain scale. Where information on risk of bias related to unpublished data or correspondence with a trialist, we noted this in the Characteristics of included studies table.

We analyzed dichotomous data (mortality, pneumonia, vomiting, and adverse events) as risk ratios (RR) with 95% confidence intervals (CIs), and continuous data (length of hospital stay, number of hours to reach the target calorie levels, and volume aspirated from stomach) as mean differences (MD), with 95% CIs. For rate outcomes, results were expressed as rate ratios with 95% CIs. We ensured that higher scores for continuous outcomes had the same meaning for the particular outcome, explained the direction to the reader, and reported where the directions were reversed if this was necessary (Review Manager 2014).

We undertook meta‐analyses only where this was meaningful: if the treatments, participants, and the underlying clinical question had a high degree of similarity and were conducive to data pooling.

A common way that trialists indicated they had skewed data was by reporting medians and interquartile ranges. When we encountered this, we noted that the data were skewed and considered the implication of this. If the data were skewed, we did not perform a meta‐analysis, but provided a narrative summary instead.

We planned to include only the relevant arms if there were multiple trial arms in a single trial. If two comparisons (e.g. frequent monitoring of GRV less than four hours versus between four and eight hours and more than eight hours) must have been entered into the same meta‐analysis, we halved the control group to avoid double‐counting.

We identified no relevant cluster‐RCTs for inclusion in this review. For review updates, for dichotomous data extracted from cluster‐RCTs, we plan to account for the design effect, and calculate effective sample size and number of events using the ICC, the mean cluster size for dichotomous data, and adjusted standard errors if they have been reported, as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021). If we are unable to obtain the ICC from study reports, we will use the ICC of similar studies as a substitute. For continuous data only, the sample size will be reduced, while means and standard deviations will remain unchanged (Higgins 2021).

Similarly, identified no randomized cross‐over trials in this review. For review updates, we planned to only include data from the first period (i.e. before crossover). If we include multiple‐arm studies in the future, we intend to only extract and analyze data from the relevant study arms.

To avoid double counting of events, we considered how to report adverse events (i.e. as single events or included in a group of events). For count data (for events that occur more than once in one participant), we used the counts of rare events as a rate ratio and the counts of more common events as continuous data. Otherwise, we used dichotomous data with participants as the unit of analysis.

We contacted the study investigators to obtain missing outcome data. In cases where that failed, we did not impute for dichotomous outcomes; for continuous outcomes, we imputed the mean from the median (i.e. considered median as the mean) and the standard deviation from the standard error, interquartile range, or P values, according to the guidelines in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021). 

We used the I² statistic to measure heterogeneity among trials in each analysis (Higgins 2003). If we identified substantial heterogeneity as per the Cochrane Handbook for Systematic Reviews of Interventions (I² > 50%) (Higgins 2021), we explored the extent of such statistical heterogeneity by conducting subgroup analysis (Subgroup analysis and investigation of heterogeneity). We also assessed heterogeneity by evaluating whether there was an acceptable overlap of CIs.

For review updates, if we are able to include more than 10 trials, we will create and examine a funnel plot for possible publication bias. We will use the Egger's test to determine the statistical significance of the reporting bias, with P < 0.05 to be set for statistical significance (Egger 1997).

We used the random‐effects model for data synthesis by default. To test the robustness of our findings regardless of which analytical method was chosen, we conducted a sensitivity analysis for primary outcomes using fixed‐effect models. In case of divergence between the two models, we presented both results; otherwise, we presented only results from the random‐effects model.

We planned to carry out the following subgroup analyses using the Cochrane's Q test for subgroup interactions:

• population subsets/settings (ICU, non‐ICU (general hospital wards), or outpatients);

• participants with a high severity of illness score as defined by a validated severity scale specific to critical care (such as the Acute Physiology and Chronic Health Evaluation (APACHE), Simplified Acute Physiology Score (SAPS), or the Sequential Organ Failure Assessment (SOFA));

• obesity status (as defined in each of the included studies);

• methods used for monitoring GRV, such as aspiration from a nasogastric tube or a gastrostomy tube, ultrasound exam, and CT scans.

The a priori subgroups were designed to assess the following primary outcomes:

• mortality (at end of follow‐up);

• pneumonia (by study investigators' definition; follow‐up from EN initiation until discontinued);

• vomiting (as per study authors' definition; follow‐up from EN initiation to discontinuation).

We performed the following sensitivity analyses to assess the robustness of our conclusions for the primary outcomes:

• comparison based on our risk of bias assessment of included studies where we excluded low‐certainty (high risk of selection bias) studies;

• comparison of results synthesized from a fixed‐effect versus those from a random‐effects model;

• excluding trials for which means or standard deviations or both were imputed.

We created summary of findings tables with the following outcomes: mortality, pneumonia, and length of hospital stay. These tables provide important information on the certainty of the evidence, the magnitude of the intervention effects, and the total available data on the main outcomes (Schünemann 2011a). We used the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to assess the certainty of the evidence on the studies that contributed data for each outcome, classifying the certainty as 'high', 'moderate', 'low', or 'very low' (Guyatt 2008; Guyatt 2011; Schünemann 2011b). When considering treatment effects, we took into account the risk of bias for the studies that contributed to that outcome (Assessment of risk of bias in included studies). Two review authors (NK, RY) independently assessed the certainty of the evidence for each study using the methods and recommendations described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021), using GRADEpro GDT software (GRADEpro GDT). We justified all decisions to downgrade or upgrade the certainty of the evidence in the footnotes and provided comments to aid the reader's understanding of the review where necessary. We considered whether there was additional outcome information that was not incorporated into the meta‐analyses, noted this in the comments, and stated if it supported or contradicted the information from the meta‐analyses.