Nutrition support in hospitalised adults at nutritional risk
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the benefits and harms of nutrition support versus no intervention, treatment as usual, or placebo in hospitalised adults at nutritional risk.
Background
The prevalence of disease‐related malnutrition in Western European hospitals is estimated to be about 30% (Norman 2008). To date, there is no consensus whether poor nutritional status causes poorer clinical outcome or if it is merely associated with it. A poor nutritional status might be a consequence of the underlying disease rather than a cause of poor clinical outcome. If this is the case, focusing on nutrition support might be futile.
One meta‐analysis from 2003 analysing randomised clinical trials of enteral nutrition (tube feeding or oral supplements) found a 50% reduction in complications when trials including diverse patient groups were aggregated in a single analysis (Stratton 2003). However, this analysis did not assess the risks of bias in the included trials. One systematic review assessing the effect of enteral or volitional nutrition versus untreated controls assessed risk of bias in the included trials in terms of allocation concealment and blinding (Koretz 2007). However, the review did not assess incomplete outcome data, selective outcome reporting, or for‐profit bias (Wood 2008; Higgins 2011; Savović 2012a). In spite of these caveats, the systematic review showed that enteral nutrition did not seem to benefit any subgroup of people except geriatric participants (Koretz 2007). There was no aggregated analysis of all the trials (Higgins 2011). A different meta‐analysis (Stratton 2007) looked at people having abdominal surgery. Despite the fact that both Koretz 2007 and Stratton 2007 included people having abdominal surgery they reached opposing conclusions. The first meta‐analysis showed no benefit of enteral nutrition on people having abdominal surgery. The second meta‐analysis showed benefit of both oral and enteral nutrition support. Yet another systematic review assessed the effects of parenteral nutrition support versus no nutrient intake (Koretz 2001). This review concluded that there were not enough data to assess whether parenteral nutrition had any effect in people being either severely malnourished or with a high rate of catabolism(i.e., in people at nutritional risk). The overall results showed no significant beneficial effect of parenteral nutrition, except preoperatively (Koretz 2001). One more recent systematic review and meta‐analysis looking at enteral nutrition for people in intensive care units concluded that only trials with a high risk of bias showed reduced mortality (Koretz 2014).
Description of the condition
Malnutrition consists of two complex components: 1. Insufficient delivery of nutrients that may be due to low consumption, low absorption of nutrients through the gastrointestinal tract, failure to utilise the absorbed nutrients, or an increase in excretion of nutrients; and 2. increased catabolism that may be due to an underlying disease or a consequent treatment. The many adverse outcomes associated with malnutrition include malfunctioning of the immune system, impaired wound healing, muscle wasting, longer lengths of hospital stay, higher treatment costs, and increased mortality (Barker 2011).
Numerous screening tools, anthropometric measurements, biomarkers, and conditions have been proposed to identify people at nutritional risk. Three of the main screening tools devised are the nutritional risk screening 2002 (NRS 2002) (Kondrup 2003), the malnutrition universal screening tool (MUST) (Elia 2003), and the mini nutritional assessment (MNA) (Vellas 1999). The subjective global assessment (SGA) (Detsky 1987) is an assessment tool that aims at predicting clinical outcome (van Bokhorst 2014). The NRS, MUST, and MNA screening tools do not distinguish between being at risk of malnutrition and being malnourished, whereas the SGA aims only at identifying people who are malnourished. Although not entirely similar, the screening tools, including the SGA, use many of the same questions and focus on identifying people at nutritional risk.
The screening tools look at two aspects of being at nutritional risk. The first aspect is whether the person is malnourished presently, and the second is whether the person might become malnourished in the future. Body mass index (BMI), weight loss during the last three or six months, and food intake during the last week are all variables assessed when determining if a person is currently malnourished. The assumption that the person might become malnourished in the future is based on an association between certain conditions and nutritional requirements. The mechanism of action is thought to be a high rate of catabolism either directly associated to the condition or the consequent treatment leading to an increased protein requirement. A low intake of food might contribute. Examples of such conditions and interventions are open major abdominal surgery (Morlion 1998); stroke (Chalela 2004); severe infections, defined as sepsis with organ dysfunction (Shaw 1987); people in intensive care units with organ failure (Larsson 1990); and sick elderly people (Hickson 2006; Norman 2008). In these conditions, protein requirement to maintain nitrogen balance, if possible at all, is approximately 1.2 g/kg per day or more.
Biomarkers and anthropometric measures have also been used to define nutritional risk (van Bokhorst 2014). The biomarkers include low levels of albumin, low levels of other plasma proteins, and low lymphocyte counts (van Bokhorst 2014). It is questionable if the biomarkers are directly related to being at nutritional risk (van Bokhorst 2014). The anthropometric measures include, in addition to body weight and height or BMI, triceps skinfold and arm muscle circumference.
Description of the intervention
The intention with all forms of nutrition is to increase uptake of essential nutrients. The nutrition support can come in many different forms. One special type of nutrition support is immuno‐nutrition, which contains nutrients believed to possess specific properties (e.g. immune modulating). Examples of such nutrients are ribonucleic acid, enhanced amounts of glutamine, and arginine.
The five main ways of administration may be classified as 'general nutrition support', 'fortified foods', 'oral nutrition supplements', 'enteral nutrition', and 'parenteral nutrition' (Lochs 2006). 'General nutrition support' aims at increasing normal food consumption. It includes, but is not limited to, dietary counselling and usually involves an estimation of the person's requirements and guidance of the person as to which food items that might be suitable. 'Fortified foods' are normal food enriched with specific nutrients, in particular with energy and proteins with or without additional vitamins, minerals, and trace elements (Lochs 2006). 'Oral nutrition supplements' are supplementary oral intake of food for special medical purposes in addition to the normal food. Oral nutrition supplements are usually liquid, but they are also available in other forms such as powder, dessert‐style, or bars (Lochs 2006). 'Enteral nutrition' is the infusion of a standard liquid formulation through a tube into either the stomach or the small intestine. 'Parenteral nutrition' is intravenous fluids containing both a source of nitrogen and a non‐protein calorie source as well as all essential nutrients.
How the intervention might work
Being nutritionally at risk consists of two complex components (see Description of the condition). The result is that the cells and organs of the body are thought to function sub‐optimally. The main focus of nutrition support is to provide essential nutrients in order to preserve or restore normal functions of a variety of cells and organs, which might improve clinical outcomes, (i.e., fewer complications, fewer infections, earlier mobilisation, shorter length of hospital stay, and improved quality of life; Stratton 2003).
Why it is important to do this review
The prevalence of disease‐related malnutrition in hospitals is considerable. A substantial disease‐burden and healthcare cost can be alleviated by nutrition support if it is effective and, reciprocally, a considerable cost and a number of complications associated with nutrition support can be prevented if it is ineffective or even harmful. Nutrition support might have beneficial effects in people at risk of malnutrition but previous meta‐analyses have shown conflicting results (Stratton 2003; Koretz 2007; Stratton 2007; Koretz 2014), and have not exclusively included participants with an indication for nutrition support (Koretz 2007). No systematic review exists that fully takes into account the risk of systematic errors due to bias (overestimation of benefits and underestimation of harms), the risks of systematic errors due to design errors, and risks of random errors ('play of chance') (Keus 2010). We intend to focus on adults with malnutrition or at risk of malnutrition because this population theoretically has the largest potential to benefit from nutrition support.
Objectives
To assess the benefits and harms of nutrition support versus no intervention, treatment as usual, or placebo in hospitalised adults at nutritional risk.
Methods
Criteria for considering studies for this review
Types of studies
We will include all randomised clinical trials irrespective of publication type, publication status, publication date, or language. For harms, we will also include observational studies identified during our searches for randomised clinical trials. If such observational studies are too numerous, we may decide to split the assessments of those studies into a focused review on harms in observational studies.
Types of participants
Adults hospitalised at the beginning of the intervention period fulfilling one or more of the following inclusion criteria and none of the exclusion criteria.
Inclusion criteria
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Adults characterised as at nutritional risk according to the NRS 2002, MUST, MNA, or SGA criteria (see Background).
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Adults characterised as moderately at risk of malnutrition according to the screening tool NRS 2002 (i.e., BMI less than 20.5 kg/m2, weight loss of at least 5% during the last three months, weight loss of at least 10% during the last six months, or insufficient food intake during the last week (50% of requirement or less) (Kondrup 2003).
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Adults theoretically known to be at nutritional risk either due to increased nutritional requirements or decreased food intake. We will accept the following conditions and procedures: major surgery such as open abdominal (liver, pancreas, gastro‐oesophageal, small intestine, colorectal) surgery; stroke; adults in intensive care units; adults with severe infections, and frail elderly people (defined by trialists) with pulmonary disease, oncology, or minor surgery (e.g. hip fracture) (Shaw 1987; Larsson 1990; Morlion 1998; Chalela 2004; Norman 2008). It is possible that we will find conditions or procedures with elevated protein requirements that we have not listed above that will need to be added on a post‐hoc basis.
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Adults characterised as nutritionally at risk due to surrogate biomarkers such as low levels of albumin, low levels of other plasma proteins, or low lymphocytes counts or anthropometric markers (BMI, triceps skinfold, arm muscle circumference).
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Adults characterised by the trialists as malnourished, undernourished, at nutritional risk, or similar terms but that is reached using a classification not mentioned above.
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Adults characterised by the trialists as malnourished, undernourished, at nutritional risk, or similar terms but that is not specified how this classification is reached.
Exclusion criteria
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Children or adolescents.
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Pregnant or lactating women.
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People receiving dialysis.
Traditionally, trials with participants under the age of 18 years old, pregnant and lactating women, or people receiving dialysis are investigated in separate reviews. Therefore, we will not include such participants in the present systematic review.
Types of interventions
Nutrition support (experimental group)
We will accept any intervention that the trialists classify as nutrition support, nutritional support, or in similar terms. As mentioned in the Description of the intervention, nutrition support may include general nutrition support, fortified foods, oral supplements, enteral nutrition, and parenteral nutrition.
We will not include the following interventions: immuno‐nutrition, glutamine only as the primary intervention, vitamin supplementation only, or similar non‐standard nutrition support interventions.
Control group
We will accept 'no intervention', placebo, or treatment as usual (any type of non‐specific supportive intervention such as 'treatment as usual', 'standard care', or 'clinical management') as control interventions (Jakobsen 2011). We will not accept enteral nutrition and parenteral nutrition as treatment as usual.
Co‐interventions
We will allow any co‐intervention but only if the co‐intervention is intended to be delivered similarly to both the experimental group and the control group (Jakobsen 2013).
Types of outcome measures
We will estimate all continuous and dichotomous outcomes at two time points:
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At the end of the trial intervention period (defined according to the trialists). This is the most important outcome measure time point in this review. We anticipate that nutrition support will have an effect already during the intervention period because it may work as a buffer to the condition of the participant.
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At maximum follow‐up.
Primary outcomes
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All‐cause mortality (dichotomous outcome).
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Number of participants with serious adverse events (dichotomous outcome). We will use the International Conference on Harmonisation (ICH) Guidelines for Good Clinical Practice's definition of a serious adverse event (ICH‐GCP 1997), that is, any untoward medical occurrence that results in death, is life threatening, requires hospitalisation or prolongation of existing hospitalisation, results in persistent or significant disability or incapacity, or is a congenital anomaly or birth defect. We will consider all other adverse events as non‐serious.
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Quality of life measured on any valid scale, such as 36‐item Short Form (SF‐36) (Ware 1992) (continuous outcome).
Secondary outcomes
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Time to death (survival data).
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Number of participants with morbidity (as defined by the trialists) (dichotomous outcome).
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BMI (continuous outcome).
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Weight (continuous outcome).
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Hand‐grip strength (continuous outcome).
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Six‐minute walking distance (continuous outcome).
Search methods for identification of studies
Electronic searches
We will search the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, EMBASE, LILACS, and Science Citation Index Expanded (Royle 2003) in order to identify relevant trials. The preliminary search strategies with the expected time spans of the searches are given in Appendix 1. In addition, we will search the World Health Organization International Clinical Trials Registry Platform (www.who.int/ictrp); clinicaltrials.gov; Turning Research Into Practice (TRIP); Google Scholar; and BIOSIS.
Searching other resources
We will identify and include where relevant the bibliographies of review articles and identified trials by searching SciSearch, and personal files.
Data collection and analysis
We will perform the review following the recommendations of The Cochrane Collaboration (Higgins 2011) and the Cochrane Hepato‐Biliary Group Module (Gluud 2014). We will perform the analyses using Review Manager 5 (RevMan 2012), STATA 13 (Stata 2013), and Trial Sequential Analysis (CTU 2011). We will present a table describing the types of serious adverse events in each trial.
Selection of studies
Two review authors (EEN and JF) will independently evaluate the identified articles. If a trial is identified as relevant by one author, but not by the other, the two authors will discuss the reasoning behind their decision. If the two authors still disagree, a third author (JCJ) will resolve the issue.
Data extraction and management
Two review authors will independently extract and validate data using data extraction forms that will be designed for the purpose. The two authors will discuss any disagreement concerning the extracted data. If the two authors still disagree, a third author (JCJ) will resolve the issue. In case of relevant data not being available, we will contact the trial authors.
Assessment of risk of bias in included studies
Two review authors (JF and another author) will independently assess the risk of bias of each included trial according to the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), the Cochrane Hepato‐Biliary Group Module (Gluud 2015), and methodological studies (Schulz 1995; Moher 1998; Kjaergard 2001; Gluud 2006; Wood 2008; Lundh 2012; Savović 2012a; Savović 2012b). We will use the following definitions in the assessment of risk of bias.
Allocation sequence generation
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Low risk of bias: sequence generation was achieved using computer random number generation or a random number table. Drawing lots, tossing a coin, shuffling cards, and throwing dice were adequate if performed by an independent person not otherwise involved in the trial.
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Uncertain risk of bias: the method of sequence generation was not specified.
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High risk of bias: the sequence generation method was not random or only quasi‐randomised. We will only use these studies for the assessments of harms and not for benefits.
Allocation concealment
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Low risk of bias: the participant allocations could not have been foreseen in advance of, or during, enrolment. Allocation was controlled by a central and independent randomisation unit, on‐site locked computer, identically looking numbered sealed opaque envelopes, drug bottles or containers prepared by an independent pharmacist or investigator. The allocation sequence was unknown to the investigators.
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Uncertain risk of bias: the method used to conceal the allocation was not described so that intervention allocations may have been foreseen in advance of, or during, enrolment.
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High risk of bias: the allocation sequence was likely to be known to the investigators who assigned the participants. We will only use these studies for the assessments of harms and not for benefits.
Blinding of participants and treatment providers
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Low risk of bias: it was mentioned that both participants and personnel providing the interventions were blinded and this was described.
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Uncertain risk of bias: it was not mentioned if the trial was blinded, or the extent of blinding was insufficiently described.
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High risk of bias: no blinding or incomplete blinding was performed.
Blinding of outcome assessment
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Low risk of bias: it was mentioned that both participants and outcome assessors were blinded and this was described.
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Uncertain risk of bias: it was not mentioned if the trial was blinded, or the extent of blinding was insufficiently described.
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High risk of bias: no blinding or incomplete blinding was performed.
Incomplete outcome data
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Low risk of bias: missing data were unlikely to make treatment effects depart from plausible values. This could either be 1. there were no drop‐outs or withdrawals for all outcomes, or 2. the numbers and reasons for the withdrawals and drop‐outs for all outcomes were clearly stated, could be described as being similar in both groups, and the trial handled missing data appropriately in an intention‐to‐treat analysis using proper methods(e.g. multiple imputations)*. Generally, the trial is judged as at a low risk of bias due to incomplete outcome data if drop‐outs are less than 5%. However, the 5% cut‐off is not definitive.
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Uncertain risk of bias: there was insufficient information to assess whether missing data were likely to induce bias on the results.
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High risk of bias: the results were likely to be biased due to missing data either because the pattern of drop‐outs could be described as being different in the two intervention groups or the trial used improper methods in dealing with the missing data (e.g. last observation carried forward).
* Multiple imputation is a general approach to the problem of missing data. It aims to allow for the uncertainty about the missing data by creating several different plausible imputed data sets and appropriately combining results obtained from each of them. The first stage is to create multiple copies of the data set, with the missing values replaced by imputed values. These are sampled from their predictive distribution based on the observed data ‐ thus multiple imputation is based on a Bayesian approach. The imputation procedure must fully account for all uncertainty in predicting the missing values by injecting appropriate variability into the multiple imputed values. The second stage is to use standard statistical methods to fit the model of interest to each of the imputed data sets. The estimated associations from the imputed data sets will differ and are only useful when a mean is used to give overall estimated associations. Valid inferences are obtained because we obtain a mean over the distribution of the missing data given the observed data (Sterne 2009).
Selective outcome reporting
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Low risk of bias: a protocol was published before or at the time, the trial was begun and the outcomes called for in the protocol were reported on. If there is no protocol or the protocol was published after the trial has begun, reporting of all‐cause mortality and serious adverse events will grant the trial a grade of low risk of bias.
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Uncertain risk of bias: no protocol was published and the outcomes all‐cause mortality and serious adverse events were not reported on.
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High risk of bias: the outcomes in the protocol were not reported on.
For‐profit bias
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Low risk of bias: the trial appeared to be free of industry sponsorship or other type of for‐profit support that may manipulate the trial design, conductance, or results of the trial.
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Uncertain risk of bias: the trial may or may not be free of for‐profit bias as no information on clinical trial support or sponsorship was provided.
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High risk of bias: the trial was sponsored by industry or received other type of for‐profit support.
Other bias
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Low risk of bias: the trial appeared to be free of other bias domains (e.g. academic bias) that could put it at risk of bias.
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Uncertain risk of bias: the trial may or may not have been free of other domains that could put it at risk of bias.
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High risk of bias: there were other factors in the trial that could put it at risk of bias (e.g. authors have conducted trials on the same topic).
Overall risk of bias
We will judge trials to be at a low risk of bias if they are assessed as at a low risk of bias in all the above domains. We will judge trials to be at a high risk of bias if they are assessed as having an uncertain risk of bias or a high risk of bias in one or more of the above domains. We will assess the domains 'blinding of outcome assessment' and 'incomplete outcome data' for each outcome. Thus, we will be able to assess the bias risk for each result in addition to each trial. The results of our primary outcomes with a low risk of bias will be our primary analyses.
Measures of treatment effect
Dichotomous outcomes
We will calculate risk ratios (RR) with 95% confidence intervals (CI) for dichotomous outcomes.
Continuous outcomes
We will include both follow‐up scores and change scores in the analyses. We will use follow‐up scores in the analyses if both are reported. We will calculate the mean differences (MD) and the standardised mean difference (SMD) with 95% CI for continuous outcomes.
Survival data
We will analysed survival data using estimates of log hazard ratios and standard errors. If the trialists do not report these data, we will calculate the log hazard ratios and standard errors if possible (Higgins 2011). We will use the generic inverse‐variance method to meta‐analyse survival data (see Section 9.4.3.2 of the Cochrane Handbook for Systematic Reviews of Interventions; Higgins 2011)
Dealing with missing data
Dichotomous outcomes
If the trialists used proper methodology (e.g. multiple imputation) to deal with missing data, we will use these data in our primary analysis. We will not use intention‐to‐treat data if the original report did not contain it. We will not impute missing values for any outcomes in our primary analysis. In two of our sensitivity analyses, we will impute data (see 'Sensitivity analysis').
Continuous outcomes
If trialists used proper methodology (e.g. multiple imputation) to deal with missing data, we will use these data in our primary analysis. We will primarily use follow‐up scores. If only change values are reported, we will analyse the results together with follow‐up scores (Higgins 2011). If standard deviations (SD) are not reported, we will calculate the SDs using data from the trial if possible. We will not use intention‐to‐treat data if the original report did not contain such data. We will not impute missing values for any outcomes in our primary analysis. In our sensitivity analysis for continuous outcomes, we will impute data, see 'Sensitivity analysis'.
Sensitivity analysis
To assess the potential impact of the missing data for dichotomous outcomes, we will perform the two following sensitivity analyses.
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'Best‐worst‐case' scenario: we will assume that all participants lost to follow‐up in the experimental group have survived, have had no serious adverse event, and have had no morbidity; and all those participants with missing outcomes in the control group have not survived, have had a serious adverse event, and have had morbidity.
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'Worst‐best‐case' scenario: we will assume that all participants lost to follow‐up in the experimental group survived, had a serious adverse event, and had morbidity; and that all those participants lost to follow‐up in the control group had survived, had no serious adverse event, and had no morbidity.
We will present results from both scenarios in our review.
To assess the potential impact of missing SDs for continuous outcomes, we will perform the following sensitivity analysis.
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Where SDs are missing and it is not possible to calculate them, we will impute SDs from trials with similar populations and low risk of bias. If we find no such trials, we will impute SDs from trials with a similar population. As the final option, we will impute SDs from all trials.
We will present results from the scenario in our publication.
Assessment of heterogeneity
We will assess the presence of statistical heterogeneity using the Chi2 test with significance set at P value < 0.10 and measure the quantities of heterogeneity using the I2 statistic (Higgins 2002; Higgins 2003). We will also perform a forest plot to illustrate any heterogeneity visually.
Assessment of reporting biases
We will use a funnel plot to assess reporting bias if we include 10 or more trials. Using the asymmetry of the funnel plot, we will assess the risk of bias. For dichotomous outcomes, we will test asymmetry using the Harbord test (Harbord 2006). For continuous outcomes, we will use the regression asymmetry test (Egger 1997) and the adjusted rank correlation (Begg 1994).
Data synthesis
We will base our primary conclusions on the results of the primary outcomes with a low risk of bias at the end of intervention. We will consider the results of our primary outcomes with high risk of bias, secondary outcomes, outcomes at maximum follow‐up, sensitivity analyses, and subgroup analyses as hypothesis generating tests (Jakobsen 2014).
Meta‐analysis
We will undertake this meta‐analysis according to the recommendations stated in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will use the statistical software Review Manager 5 provided by The Cochrane Collaboration to analyse data (RevMan 2012). Where data are only available from one trial, we will use Fisher's exact test for dichotomous data (Fisher 1922), and Student's t‐test for continuous data (Student 1908).
Assessment of significance
We will assess our intervention effects with both random‐effects model meta‐analyses (DerSimonian 1986) and fixed‐effect model meta‐analyses (DeMets 1987). We will use the more conservative point estimate of the two (Jakobsen 2014). The more conservative point estimate is the estimate closest to zero effect. If the two estimates are equal, we will use the estimate with the widest CI. We use three primary outcomes and, therefore, we will consider a P value of 0.03 or less as statistically significant (Jakobsen 2014). We will use the eight‐step procedure to assess if the thresholds for significance are crossed (Jakobsen 2014).
Trial sequential analysis
Traditional meta‐analysis runs the risk of random errors due to sparse data and repetitive testing of accumulating data when updating reviews. Therefore, we will perform trial sequential analyses (CTU 2011; Thorlund 2011) on the outcomes in order to calculate the required information size and the breach of the cumulative Z‐curve of the relevant trial sequential monitoring boundaries (Brok 2008; Wetterslev 2008; Brok 2009; Thorlund 2009; Wetterslev 2009; Thorlund 2010). Hereby we wish to control the risks of type I errors and type II errors. A more detailed description of trial sequential analysis can be found at www.ctu.dk/tsa/ (Thorlund 2011).
For dichotomous outcomes, we will estimate the required information size based on the proportion of participants with an outcome in the control group, a relative risk reduction of 20%, an alpha of 3% (Jakobsen 2014), a beta of 20%, and the diversity suggested by the trials in the meta‐analysis. For continuous outcomes, we will estimate the required information size based on the SD observed in the control group of trials with low risk of bias and a minimal relevant difference of 50% of this SD, an alpha of 3%, a beta of 20%, and the diversity suggested by the trials in the meta‐analysis.
Subgroup analysis and investigation of heterogeneity
Below we list a very large number of subgroup analysis. Such a large number will create risks for type I errors and type II errors. Accordingly, we will interpret our subgroup findings conservatively.
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Outcomes at a low risk of bias compared to outcomes at a high risk of bias.
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Comparison of trials assessing the effects of the following interventions:
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general nutrition support;
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fortified foods;
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oral nutrition support;
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enteral nutrition;
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parenteral nutrition.
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Comparison of trials assessing the effects of nutrition support in the following medical specialities:
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cardiology;
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medical gastroenterology and hepatology;
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geriatrics;
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pulmonary disease;
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endocrinology;
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infectious diseases;
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rheumatology;
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haematology;
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nephrology;
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gastroenterological surgery;
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trauma surgery;
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orthopaedics;
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plastic, reconstructive, and aesthetic surgery;
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vascular surgery;
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transplant surgery;
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urology;
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thoracic surgery;
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neurological surgery;
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oro‐maxillo‐facial surgery;
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anaesthesiology;
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emergency medicine;
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psychiatry;
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neurology;
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oncology;
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dermatology;
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gynaecology.
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Comparison of trials where the experimental and control group receive the following (see definitions of 'adequate' and 'inadequate' in the paragraphs below):
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trials where the experimental group receives clearly adequate nutrition and the control group receives clearly inadequate nutrition;
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trials where the experimental group does not receive an inadequate amount of nutrition or the control group receives an adequate amount of nutrition, or both;
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trials where the experimental group is overfed;
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trials where the calorie and protein intake in the experimental group and the control group cannot be obtained from the publications or the study authors.
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We define adequate intake in experimental groups to be 80% to 120% of estimated energy expenditure (i.e., adequate range then is 20 to 30 kcal/kg per day in bedridden participants (including participants in intensive care units).
We define inadequate intake as less than 80% of the resting energy expenditure (i.e., inadequate intake is less than 20 kcal/kg per day in bedridden participants).
We define overfeeding as intakes greater than 35 kcal/kg per day except in trials where participants have a known extraordinary energy requirement (e.g. participants with a temperature of 40 °C, participants with extensive burns, participants with unusually high physical activity, etc.).
The resting energy expenditure can either be given in the trial or calculated by us using the Harris‐Benedict equation, based on data in the randomised clinical trial (height, weight, age, sex) (Harris 1918).
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Comparison of trials where the participants are characterised as 'at nutritional risk' by the following screening tools:
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NRS 2002;
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MUST;
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MNA;
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SGA;
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participants characterised as 'at nutritional risk' by other means.
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Comparison of trials where the participants are characterised as 'at nutritional risk' due to the following conditions:
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major surgery such as open abdominal (liver, pancreas, gastro‐oesophageal, small intestine, colorectal) surgery;
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stroke;
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people in intensive care units including trauma;
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people with severe infections;
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frail elderly people (aged 65 years or over, as mean age of participants) with less severe conditions that are known to increase protein requirements moderately;
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participants who do not fall into one of the above categories.
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Comparison of trials where the participants are characterised as 'at nutritional risk' due to the following criteria:
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BMI less than 20.5 kg/m2;
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weight loss of at least 5% during the last three months;
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weight loss of at least 10% during the last six months;
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insufficient food intake during the last week (50% of requirement or less);
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participants characterised as 'at nutritional risk' by other means.
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Comparison of trials where the participants are characterised as 'at nutritional risk' due to the following biomarkers or anthropometric measures:
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biomarkers;
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anthropometric measures;
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participants characterised as 'at nutritional risk' by other means.
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Comparison of trials published (the date when randomisation began will be used if this is reported) in the following time periods:
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before 1960;
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1960 to 1979;
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1980 to 1999;
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after 1999.
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Comparison of trials where the interventions lasts fewer than three days compared to trials where the interventions lasts three days or more.
'Summary of findings' table
We will use the GRADE system (Guyatt 2008) to assess the quality of the body of evidence associated with each of the major outcomes in our review constructing 'Summary of findings' tables using GRADE software (ims.cochrane.org/revman/other‐resources/gradepro). The GRADE approach appraises the quality of a body of evidence based on the extent to which one can be confident that an estimate of effect or association reflects the item being assessed. The quality measure of a body of evidence considers within study risk of bias, indirectness of evidence, heterogeneity of data, imprecision of effect estimates, and risk of publication bias.
