This is an electronic version of an article published
in the American Journal of Gastroenterology 2007;102(2):412-429.
Does enteral nutrition affect clinical outcome?
A systematic review of the randomized trials
Ronald L. Koretz, M.D.
Olive View-UCLA Medical Center
Alison Avenell, M.D., M.R.C.P., F.R.C. Path., M.B., B.S., M.Sc.
Health Services Research Unit*
University of Aberdeen
Timothy O. Lipman, M.D.
Veterans Affairs Medical Center
Carol L. Braunschweig, Ph.D., R.D.
University of Illinois at Chicago
Anne C. Milne, M.Sc., S.R.D.
Health Services Research Unit*
University of Aberdeen
Submitted August 31, 2006
Address communication to:
Ronald L. Koretz, M.D.
Department of Medicine
Olive View-UCLA Medical Center
14445 Olive View Drive
Sylmar, California 91342
* The Health Services Research Unit is core funded by the Chief Scientist Office of the Scottish
Executive Health Department; however, the views expressed here are those of the authors.
1. Because malnourished patients have poorer outcomes than do nourished ones, artificial nutrition is
employed in order to improve the clinical outcome.
2. Randomized trials of parenteral nutrition have largely been unable to show that this therapy improves
the clinical outcome, and have even suggested that the therapy is associated with net harm (especially in
patients undergoing cancer chemo- or radiation therapy).
What is new:
1. Randomized trials of low quality have indicated that nutritional supplements, taken orally, improve
survival in malnourished geriatric patients who are in institutions (including hospitals). Two trials of high
quality found effects in the same direction, but failed to achieve statistical significance.
2. Randomized trials of low quality have suggested that enteral nutrition may reduce infection rates in
critically ill patients and improve outcome in low-birth-weight infants (when provided as “trophic
3. Randomized trials of low quality have suggested that both enteral nutrition and oral supplements may
be helpful in the postoperative situation and in patients with chronic liver disease.
4. Two large high quality randomized trials found that there is no benefit in providing enteral nutrition in
the first week to patients with strokes associated with dysphagia or in providing supplements to stroke
patients who do not have dysphagia.
5. Low quality randomized trials have failed to demonstrate any utility from EN in the non-surgical
treatment of cancer patients, or in the treatment of patients with inflammatory bowel disease or hip
6. Low quality randomized trials have failed to demonstrate any utility from oral supplements in the non-
surgical treatment of cancer patients or in patients with chronic pulmonary disease or hip fractures.
7. There are no or inadequate data from randomized trials to assess the use of enteral nutrition or oral
supplements in any other diseases.
Background: Both parenteral nutrition (PN) and enteral nutrition (EN) are widely advocated as
adjunctive care in patients with various diseases. A systematic review of 82 randomized controlled trials
(RCTs) of PN published in 2001 found little, if any, effect on mortality, morbidity, or duration of hospital
stay; in some situations, PN increased infectious complication rates. Objective: To assess the effect of
EN or volitional nutrition support (VNS) in individual disease states from available randomized
controlled trials (RCTs). Design: We conducted a systematic review. RCTs comparing EN or VNS to
untreated controls, or comparing EN to PN, were identified and separated according to the underlying
disease state. Meta-analysis was performed when at least 3 RCTs provided data. The evidence from the
RCTs was summarized into one of five grades. A or B indicated the presence of strong or weak (low
quality RCTs) evidence supporting the use of the intervention. C indicated a lack of adequate evidence to
make any decision about efficacy. D indicated that limited data could not support the intervention. E
indicated either that strong data found no effect, or that either strong or weak data suggested that the
intervention caused harm. Patients and settings: RCTs could include either hospitalized or non-
hospitalized patients. The EN or VNS had to be provided as part of a treatment plan for an underlying
disease process. Interventions: The RCT had to compare recipients of either EN or VNS to controls not
receiving any type of artificial nutrition or had to compare recipients of EN with recipients of PN.
Outcome measures: Mortality, morbidity (disease-specific), duration of hospitalization, cost, or
interventional complications. Summary of grading:
A – No indication was identified.
B – EN or VNS in the perioperative patient or in patients with chronic liver disease; EN in critically ill
patients or low birth weight infants (trophic feeding); VNS in malnourished geriatric patients. (The low
quality trials found a significant difference in survival favoring the VNS recipients in the malnourished
geriatric patient trials; two high quality trials found non-significant differences that favored VNS as well.)
C – EN or VNS in liver transplantation, cystic fibrosis, renal failure, pediatric conditions other than low
birth weight infants, well-nourished geriatric patients, non-stroke neurologic conditions, AIDS; EN in
acute pancreatitis, chronic obstructive pulmonary disease, non-malnourished geriatric patients; VNS in
inflammatory bowel disease, arthritis, cardiac disease, pregnancy, allergic patients, preoperative bowel
D – EN or VNS in patients receiving non-surgical cancer treatment or in patients with hip fractures; EN in
patients with inflammatory bowel disease; VNS in patients with chronic obstructive pulmonary disease
E – EN in the first week in dysphagic, or VNS at any time in non-dysphagic, stroke patients who are not
malnourished; dysphagia persisting for weeks will presumably ultimately require EN.
Conclusions: There is strong evidence for not using EN in the first week in dysphagic, and not using
VNS at all in non-dysphagic, stroke patients who are not malnourished. There is reasonable evidence for
using VNS in malnourished geriatric patients. The recommendations to consider EN/VNS in
perioperative/liver/critically ill/low birth weight patients are limited by the low quality of the RCTs. No
evidence could be identified to justify the use of EN/VNS in other disease states.
An association exists between malnutrition and a poor clinical outcome. Furthermore, deprivation
of nutrient intake for a long enough period of time will have adverse clinical consequences. These two
observations have led to the hypothesis that providing artificial nutrition to patients who are, or who are at
risk of becoming, malnourished, would be beneficial. However, artificial nutrition is a medical
intervention with associated risks and costs. As such, we need to know that it is efficacious. The best
way to establish efficacy is to demonstrate it in a randomized controlled trial (RCT). In 2001, a
systematic review of the RCTs of parenteral nutrition (PN) failed, with a few exceptions, to find outcome
That review considered the intravenous infusion of nutrients. While the rationale for artificial
nutrition is usually the same when it is delivered directly into the gastrointestinal tract (consumed by
mouth or infused through a tube), the physiologic mechanisms are different than when it is provided
intravenously. It would be inappropriate to extrapolate any conclusions from PN to another form of
artificial nutrition. The objective of this systematic review is to evaluate the clinical efficacy of medical
interventions that deliver nutrient formulations directly into the gastrointestinal tract through defined
orally consumed supplements (volitional nutritional support [VNS]) or via a tube (enteral nutrition [EN]).
In doing so, we focus on RCTs that evaluate the ability of such interventions to alter one or more
clinically important outcomes in specific disease states.
A protocol was written in which a priori decisions were made regarding methodology. The
terminologies used to describe study groups and the artificial nutrition formulations are defined in Table
RCTs were identified employing previously reported strategies (1); the details are available
electronically (“Literature Search Methodology”). This search was begun in 1975; in the intervening 3
decades, some efforts were made to contact authors to obtain more information about a particular study.
However, no systematic effort was undertaken to contact all authors for this systematic review. No
language restrictions were employed; when translation facilities were not available, the data from the
English abstract, as well as any interpretable data from tables, were employed. Abstracts from meetings
The RCTs that compared EN to no treatment, EN to PN, or VNS to no treatment were so
categorized within each disease state. We assessed the outcomes of mortality, total and/or infectious
complications, lengths of hospitalization, costs, interventional complications (e.g., nausea/vomiting,
diarrhea, hyperglycemia), or any of the disease-specific outcomes. A list of these specific diseases, as
well as the disease-specific outcomes, is available electronically (“Disease States Considered”). Meta-
analysis (Revman 4.2, Cochrane Collaboration) was performed when data were available from 3 or more
RCTs. (If only one or two trials were available, we thought that there would be no more insight available
from data combination by meta-analysis than could be gleaned by just assessing each trial individually.)
Any RCT meeting the following criteria was used in the respective meta-analysis:
1) The report explicitly stated that the groups were randomized; quasirandomized or cluster randomized
trials were excluded.
2) The study compared treatment groups as defined above.
3) The study reported one or more of the outcomes being sought.
4) The therapeutic intervention was employed for at least five days, during which time the control group
received only standard therapy (or PN in the comparative trials). (Since the hypothesis underlying
artificial nutrition is that the morbidity or mortality is due to malnutrition, it was assumed that it would
require at least five days to begin to reverse that process; this same assumption was made previously .)
If a report included groups of patients randomized to an untreated control and to two or more
forms of EN or VNS, all treated groups were combined and compared to the control. If a report included
groups of patients assigned to EN and to VNS, the data from the EN group were included in the EN
analysis and the data from the VNS group were included in the VNS analysis. (The same control group
was used in both analyses in this latter case.)
If dichotomous outcomes were reported as a total number instead of the number of affected
patients, it was assumed that there was one event per patient. (If the number of events was greater than
the number of patients, each patient was assigned one event.) Numerical estimates were made from
graphs when necessary.
Meta-analysis of continuous data requires knowledge of both the mean and standard deviation for
both treatment arms. Thus, the initial analyses only included trials in which these numbers were reported.
However, one of the peer reviewers of this paper pointed out a statistical method of converting the median
and range into a mean and variance (2). Thus, post facto analyses were also performed employing
continuous data from trials in which the medians and ranges were provided. Since none of those analyses
materially changed any of the estimates or conclusions, they will not be subsequently reported.
Two reviewers independently abstracted the information from each RCT onto predesigned data
summary forms. Discrepancies were resolved by consensus between the two abstractors.
Heterogeneity (i.e., adding apples and oranges) is a limitation of meta-analysis. It can be sought
with statistical tests; the Revman software calculates both Cochran’s Q (expressed as a p value) and I2
statistics (3). Statistical heterogeneity was defined as p < 0.10 or I2 > 25%. A fixed (or random) effects
model was employed when heterogeneity was absent (or present).
Dichotomous data are presented as an absolute risk difference (ARD), namely the difference
between the incidence in the treated group and that in the control group. A 95% confidence interval (CI)
that did not include 0% was considered “significant”. The term “tendency” was applied to an analysis in
which one end of a confidence interval was 0% (i.e., the confidence interval included the possibility of no
difference). A negative ARD indicates a beneficial effect associated with the treatment.
Continuous variables are reported as weighted mean differences and 95% CIs. The same rules for
significance and tendency were applied to these calculations. A negative number represents a beneficial
effect in the treated group.
RCTs with more methodologic rigor have demonstrated lower treatment effects (4, 5); this is
presumed to represent the advertent or inadvertent introduction of bias into the less rigorous trials.
“Quality” is a term that reflects the degree of rigor that was employed. Thus, each trial was graded for
quality, with the expectation that all of the studies were randomized and the large majority of them were
not blinded. A “high quality” (lower risk of bias) study was one in which either 1) the
investigators/assessors and participants were blinded, or 2) the RCT contained both an explicit description
of an adequate allocation concealment and data that were evaluable on an intent-to-treat basis. RCTs not
meeting one or the other of these criteria were categorized as low quality.
In order to explore possible sources of heterogeneity, subgroup analyses were planned. These
planned analyses are available electronically (“Analyses and subgroup analyses planned”). Those that are
relevant will be discussed.
Our primary focus is the strength of the evidence that supports the use of EN or VNS in each
disease state. These assessments (grades) are based only on data from RCTs. Nonrandomized controlled
trials are less reliable because of potential bias (6). Expert opinion is often based on incomplete
information (7-9) and/or influenced by conflicts of interest (10, 11).
The evidence was graded by the amount and quality of the RCTs that were available as well as
what effects those trials did, or did not, demonstrate. The grades ranged from A to E, with A describing a
situation in which there was a high likelihood of benefit and E indicating a high likelihood of no benefit,
or even of harm. For some conditions, a limited amount of information was available, and that
information failed to demonstrate any significant differences in outcomes. In such situations, it may be
that a true difference was present, but the numbers were too small to establish it (i.e., a type II error), or it
may be that the failure to observe a difference was due to the intervention not having an effect.
It was decided that, if at least three low quality RCTs had failed to show a difference, the
intervention would be judged to be ineffective. If only one or two RCTs were available, the total number
of patients were considered; if that total was less than 100, the evidence was classified as being
inadequate to determine the presence or absence of a benefit.
If at least 100 patients were studied, the direction of the difference was then considered. (If two
RCTs were available, the data were arithmetically combined.) If that direction was in favor of the control
group, the intervention was judged to be ineffective. If it was in favor of the treated group, a p value for
the difference was obtained. If that p value was < 0.20, it was concluded that a type II error might be
present, so the data were considered as inadequate. (Employing a one-sided test [since only benefit was
being sought] and an α error of 0.20, there is approximately an 80% power of seeing an ARD of 15%
between the two groups; since the trials were almost always of low quality, the real ARD would likely be
lower. Given the resources required [both economic and time], such an ARD would be the lowest one
that would be clinically meaningful.)
The evidence was thus divided into 5 grades:
A – One or more high quality RCTs demonstrated benefit.
B – The evidence of benefit was limited to low quality RCTs.
C – There were inadequate data to decide if benefit is present or absent. Three different scenarios could
result in a C grade: 1) no RCTs were available; 2) only one or two RCTs containing fewer than 100
patients were available; 3) 100 or more patients were available but a type II error could not be ruled out.
D – Limited evidence was not able to define a benefit. Either at least three low quality RCTs failed to
show a difference or a type II error was not likely to be present.
E – One or more high quality RCTs indicated that the intervention was not effective or that there was any
evidence that it caused harm.
As will be noted, none of the RCTs included severely malnourished individuals. Thus, these
grades will refer to studies in which the patients were not severely malnourished and would not be
deprived of nutrient intake for > 2 weeks. Although there are only limited data to allow us to know with
certainty the period of time for which such individuals can tolerate nutrient deprivation, it was previously
concluded that waiting at least 2 weeks in the non-severely malnourished patient was reasonable (1).
Summary of RCTs identified
The total number of assessed titles could not be determined; this information was not collected
during the handsearch of Index Medicus. However, each identified RCT was stored, so the total number
of RCTs from which those included in the meta-analyses were derived could be ascertained.
Only 33 of 376 RCTs of EN met our inclusion criteria (12-45); data for one of these trials were
extracted from two different abstracts (25, 26). Similarly, we included 48 of 115 RCTs comparing EN to
PN (19, 25, 26, 44, 46-92); data for three of these trials were extracted from two different papers (25, 26,
69, 70, 76, 77). Finally, 54 of 418 RCTs of VNS were included (30, 93-145).
Data from one of the EN versus PN RCTs (55) were published at least seven different times (55,
146-151). Different numbers of patients appear in each publication, and, in at least one instance, a portion
of the study was extended and additional patients were added (151). In order to avoid duplication, we
used the most recent paper (55) and supplemented any missing categories of data with information from
the other publications. The details of the 135 RCTs employed in the various meta-analyses (“Study
Characteristics”), as well as the excluded trials and the reason(s) for exclusion (“References Excluded
from Meta-analyses”), are available electronically.
The results of the meta-analyses of the perioperative RCTs (12, 13, 15, 19, 24, 27, 29, 32, 34, 36-
40, 44, 45, 48, 50, 53-56, 64-66, 71, 74, 75, 78, 81, 82, 84-87, 95, 102, 109, 115, 122, 134, 136, 138, 141)
are summarized in Table 2. No differences were seen with regard to mortality. EN, when compared to no
artificial nutrition, was not shown to reduce the rate of total/major/wound complications or postoperative
pneumonia. There were significantly fewer infections in the EN recipients as well as a tendency for fewer
intraabdominal or intrathoracic complications. The heterogeneity resolved, and the significant differences
persisted, in the low quality trials and in the trials of the patients without cancer.
EN produced better outcomes than PN. VNS provided across-the-board benefits. These
conclusions must also be tempered by the fact that the data were largely derived from low quality studies.
Several years ago, Lewis et al (152) published a meta-analysis of 11 RCTs (12, 15, 24, 34, 45,
153-158) that assessed early postoperative enteral nutrient delivery in surgical patients. These trials
utilized EN or VNS. Lewis et al noted that artificial nutrition reduced the infection rate, but suggested
that a large trial needed to be conducted. Six of these RCTs were excluded from our analyses. While our
analysis of 11 trials of mostly postoperative EN (12, 15, 24, 27, 29, 32, 34, 36, 38, 39, 45) demonstrated a
similar effect, when only the four high quality trials were considered, this observation could not be
confirmed (ARD –2% [95% CI –25%, + 21%]).
Specialized formulations containing putative immunonutrients (ω-3 fatty acids, arginine,
ribonucleic acid, and/or glutamine) are often employed. A limited database (24, 55, 109) precluded
meaningful conclusions. Such specialized EN resulted in fewer infections than did standard EN (159).
The durations of therapy in the VNS trials were analogous to those in the EN trials (days or a few
weeks). However, all of these patients were capable of orally consuming supplements. The beneficial
effect was limited to the trials of postoperative VNS and VNS in malnourished patients.
VNS also appeared to shorten hospitalization. The subgroup analyses indicated that this benefit
was limited to the trials of preoperative VNS and VNS provided to nourished patients. Given the data
regarding complications, this observation seems counterintuitive. The quality of the trials was low and
duration of hospitalization is a subjective outcome. Furthermore, one high quality (22) and four other low
quality (115, 136, 141, 160) trials that did not provide adequate information to be included in the meta-
analysis failed to find significant differences in the duration of hospitalization.
Non-surgical cancer treatment
PN causes net harm to cancer patients undergoing chemotherapy or radiation therapy (1). There
was no apparent positive or negative effect from the enteral provision of nutrients (either through a tube
[35, 43] or by volitional consumption [93, 96, 103, 126, 135]). The trials of VNS provided mortality data;
the estimated effect favored the control group (ADR +5%) but the CIs crossed 0% (-2%, +12%). Two of
the VNS trials reported data regarding the incidences of gastrointestinal toxicity; in one the treated group
had significantly more (96) and in the other the treated group had significantly fewer (135). No trials
assessed EN or VNS in hematologic malignancies. A systematic review of artificial nutrition in bone
marrow transplantation did not identify any data regarding the enteral delivery of nutrients (alone or in
comparison to PN) (161).
Chronic liver disease: The outcomes in patients with chronic liver disease that could be assessed
with meta-analysis are summarized in Table 3 (97, 113, 125, 129, 137). VNS did not have any effect on
survival. Survival was also not affected when VNS was provided with EN as a backup (162) or when
given with an anabolic steroid (163). VNS did not have a significant effect on infectious complications or
the development of hepatic encephalopathy. Although the data could not be combined, VNS did not
appear to influence the length of hospitalization (97, 113, 129). Limited information was available from
one or two trials about other outcomes. There was no effect on the subsequent development of
hepatocellular carcinoma (125) or gastrointestinal bleeding (113, 129). The VNS recipients had
significantly lower incidences of total complications in two trials (113, 129) and also may have been less
likely to develop ascites (113, 129).
EN did not appear to have any impact on liver-disease-associated morbidity (14, 17, 21, 28, 164)
nor on the length of hospitalization (14, 17, 28). Survival with EN was not different from that with PN
(79). In light of these observations, it is curious that three low quality RCTs (14, 17, 28) of EN versus no
therapy found improved survival in the treated recipients when the fixed effects model was employed.
This model was used because the p value for heterogeneity was 0.21; however, the I2 statistic was 37%
and when the random effects model was employed, this significant difference disappeared.
Branched-chain amino acids had a modest effect in treating hepatic encephalopathy but this effect
disappeared if the analysis was limited to the high quality trials (165).
Liver transplantation: No significant differences were observed (23, 90, 120).
Pancreatic disease (acute pancreatitis)
RCTs have evaluated the use of EN in acute pancreatitis, but not in pancreatic insufficiency. The
meta-analyses of five RCTs (46, 49, 67, 72, 73) comparing EN to PN are displayed in Table 4.
Predigested formulations were delivered into post-pyloric sites. EN is safer and more effective than PN, a
conclusion also reached in another systematic review (166).
There are only limited data about the absolute value of either modality. Two small studies
compared EN to no treatment; no differences in duration of hospitalization (33) or an organ failure score
(167) were seen. One RCT compared PN to no therapy in mild pancreatitis; the PN recipients had worse
outcomes (longer duration of hospitalization and more infections) (168). If PN is harmful, a comparative
trial cannot determine whether EN is better than doing nothing.
One other trial of PN should be noted (169), but it is difficult to fit these observations into the
nutrition support picture because the results seem very unlikely. The dramatic differences in mortality
(3/41 [7%] in two PN groups versus 10/23 [43%] in the controls) have not been described in any other PN
RCT. Unfortunately, only limited methodologic details were available and efforts to contact the author in
China have, to date, been unsuccessful. The term “randomization” in the Chinese literature may not have
the same meaning as in western papers (170).
No differences were observed in the durations of hospitalization between those provided with PN
and those given EN (46, 67, 72). If PN causes more complications, especially major ones, the durations
of hospitalization should not be equivalent.
Inflammatory Bowel Disease
Four RCTs compared EN to PN (59, 61, 62, 68). A meta-analysis of the three RCTs comparing
these therapies in active Crohn’s disease (59, 62, 68) found no difference in remission rates (ARD -12%
[95% CI -32%, +9%]). No differences in remission rates were seen in two RCTs that compared VNS to
PN (171, 172). No RCTs were identified comparing EN to no therapy. In the only VNS trial (173), the
data were presented as a series of subgroup analyses; the treated subgroups had fewer surgeries and days
of hospitalization, and, while the differences were not significant, a type II error may have been present.
Keeping patients with inflammatory bowel disease in a fasting state is of no benefit (1).
PN did not confer any benefit in colitis (1). Since data from the only trial comparing PN and EN
found no difference (61), it could be inferred that EN would also be ineffective. Three systematic reviews
concluded that EN is inferior to steroid therapy for treating Crohn’s disease (174-176).
If predigested formulations are less antigenic, they might be useful in Crohn’s disease. However,
no differences were seen in comparisons with formulas containing undigested protein (174, 175).
The few RCTs comparing EN to no treatment in the critically ill do not provide compelling
evidence to employ this intervention. No differences in mortality (25, 31), duration of time on the
respirator (18, 23), or length of stay in the intensive care unit (23) or hospital (25, 31) were observed.
When 3 RCTs (126 patients) were combined (18, 25, 31), EN reduced the infection rate (ARD -
17% [95% CI -31%, -3%]). However, 30% of the control patients, who were not eating by day five, were
given PN, a source of potential infection, in the largest of these trials (63 patients) (31). Another
systematic review, employing a different set of RCTs, failed to demonstrate a reduction in the infection
rate (relative risk 0.66 [95% CI 0.36, 1.22]) (177).
That same systematic review also considered early versus later intervention with artificial nutrition
and concluded that those treated within 1-2 days of admission may have had a better survival, although
the difference was not statistically significant (relative risk 0.52 [95% CI 0.25, 1.08]) (177). Most of the
RCTs included in that meta-analysis were excluded from ours because 1) the control group received the
intervention before 5 days, 2) PN was being evaluated, and/or 3) we judged the RCT not to be
Burn patients who had EN initiated at the time of admission may have had fewer episodes of
sepsis (3/10 vs 7/10, p > 0.10) (178). Those who had the EN continued during surgery had fewer wound
infections (2/40 vs 9/40, p < 0.05) (179). However, the descriptions of the randomization process were
confusing. We are told that the patients “were randomly assigned by a case-control method” (178) and
that “randomly assigned” patients were “matched” to patients whose infusions were withheld (179).
One short term (72 hours) trial assessed the ability of EN to prevent stress bleeding in ventilated
patients (180). While blood-stained nasogastric aspirates were more common in the controls, no patient
had a significant hemorrhage. A systematic review concluded that EN should not be used for this purpose
until RCTs establish efficacy (181).
Many intensivists, believing that artificial nutrition is important, have compared different
interventions. Since the trials lack an untreated control arm, it is again difficult to determine the absolute
utility of either.
RCTs comparing EN to PN (25, 26, 47, 51, 52, 57, 58, 63, 69, 70, 76, 77, 83, 88, 92) did not find
any differences in the duration of time on the respirator (47, 69, 70) or in the long-term sequelae of head-
injured patients (83, 92). The outcomes that could be assessed with meta-analysis are summarized in
Table 5. No differences were seen with regard to survival. Another systematic review, employing
different trials, made the same observation (177). However, a third one, restricted to trials with at least a
95% followup of the enrolled patients and including studies of patients not in intensive care units,
estimated that PN, compared to EN, was associated with a reduced mortality rate (182).
Should specialized formulations be employed? Two systematic reviews of RCTs comparing them
to standard formulations failed to find any difference in mortality in the critically ill (159, 183). However,
significantly fewer infectious complications were seen when specialized formulations were used.
Pulmonary disease (including cystic fibrosis)
EN had no effect on the pulmonary outcome in patients with cystic fibrosis in one RCT (16).
While non-randomized trials have suggested that nutritional interventions produce weight gain in this
disease (187), three RCTs of VNS were unable to prove this (184-186). Furthermore, we do not know if
this would translate into improved clinical outcomes (188, 189).
Ten VNS trials assessed patients with lung disease (predominantly chronic obstructive pulmonary
disease) (98, 101, 106, 121, 127, 140, 142, 190-192). One RCT reported improvements in an activity of
daily living score (192) and another described benefits in one aspect of respiratory muscle strength (191).
Otherwise, no differences were seen in exercise capacity (98, 106, 191), handgrip strength (121),
pulmonary function (98, 101, 106, 121, 127, 190), respiratory muscle strength (101, 121, 190), or quality
of life (101). Only one death was reported in all of these trials (140) and no differences were seen in the
two trials that provided data regarding total complications (140, 142). Another systematic review also
failed to find evidence supporting artificial nutrition in chronic obstructive pulmonary disease (193).
One trial of VNS (ten patients on chronic hemodialysis) reported no deaths and two patients in
each group had some complication (132).
Acquired Immunodeficiency Syndrome
Two RCTs (165 patients) compared VNS to no therapy (116, 133). No significant differences
were seen in mortality (116), infectious complications (116), CD4 counts (116), or overall quality of life
(133). However, the possibility of a type II error could not be excluded.
No trials have assessed EN. One RCT comparing VNS to PN found no differences in median
survival, CD4 counts, or overall quality of life (194). The VNS recipients had better physical functioning
in this unblinded trial. Since one RCT of protracted (2 months) PN failed to show any benefit (195), it
might be inferred that VNS also would not be useful.
No RCTs addressed the use of EN or VNS for children who are failing to grow normally. Two
small RCTs comparing EN to PN in low birth weight infants found no difference in mortality (80) or
infection rates (80, 89). A systematic review (of non-randomized trials) addressing the use of
gastrostomy or jejunostomy tubes versus oral feeding in children with cerebral palsy concluded that the
available evidence did not show that EN provided any benefit (196).
PN is often employed in low birth weight infants. A systematic review of low quality trials of
trophic feeding (providing small amounts of enteral nutrients) indicated that this intervention reduced the
time to full feeding by 2.7 days and the duration of hospitalization by 15.6 days without altering the risk
of necrotizing enterocolitis (197). However, those reviewers were concerned about methodologic
problems (absence of blinding, lack of details about the randomization processes, inability to perform
intent to treat analyses, and publication bias).
The data from meta-analyses of 16 RCTs of VNS (30, 94, 100, 104, 108, 110, 111, 117-119, 124,
128, 130, 131, 144, 145) are summarized in Table 6; these patients were almost always malnourished
and/or institutionalized (including being in hospitals). The VNS recipients had a significantly better
survival. Two of these trials (130, 131) were high quality; while the mortality rates in both of them (11%
vs 17%, 381 patients  and 5% vs 7%, 136 patients ) also favored the treatment group, neither
difference was statistically significant. No significant effect of VNS on infectious complications (the only
other outcome reported) was observed.
From study to study, some individual measures of functional status may have been improved by
the VNS. Different measures improved in different studies, and those that improved in one trial did not
necessarily improve in another. Quality of life scores were not affected.
Neither of two trials of VNS (114, 117) nor one of EN (22) found any significant differences with
regard to the development or severity of pressure ulcers. One small study of VNS (198), and another of
generic artificial nutrition (VNS, EN, or PN) (199), found no differences in healing in patients who
already had developed pressure ulcers. (In one of these trials , the further addition of arginine,
vitamin C, and zinc did improve healing as assessed by a numerical score.)
No RCTs were found addressing the use of EN in demented patients nor for providing VNS to
healthy elderly individuals.
In three trials of EN (22, 41, 42), and in six trials of VNS (99, 112, 114, 123, 139, 200) (meta-
analyses results summarized in Table 7), mortality rates, the incidences of various complications, and
various functional or quality-of-life measures were not altered. A systematic review that included
quasirandomized and unpublished trials as well as other types of supplements concluded that, while the
evidence was weak (low quality trials), these supplements may have reduced “unfavorable outcomes” (a
combination of mortality and survivors with complications) (201).
The RCTs from the “Feed Or Ordinary Diet” (FOOD) consortium represent the largest trials in
this review (20, 105). These were high quality studies that assessed patients shortly after a stroke. In one,
gastric infusions of nutrient solutions were either begun on admission or withheld for at least 7 days in
859 dysphagic patients (20). The primary outcome was long-term survival; no difference was seen. The
intervention also did not alter complication rates or duration of hospitalization.
The other one assessed VNS in 4023 nondysphagic stroke patients (105). No differences were
seen when death alone or death and poor neurologic outcome were the end-points. In a separate smaller
VNS trial, survival was no better at the time of discharge or at 3 months (107).
No specific RCTs of EN or VNS were identified.
No specific RCTs of EN or VNS were identified.
One RCT compared the use of a high-calorie VNS formulation to a “placebo” (a 1:10 dilution of
the VNS formulation) in patients with congestive heart failure (202). No differences were seen in
One systematic review assessed various interventions to increase energy and/or protein intake in
pregnant women (203). Based on observational data, no benefits or harms could be attributed to the
various nutritional interventions.
One small RCT (26 patients) of VNS in surgical patients also provided data regarding the efficacy
of the bowel preparation (141). No difference was seen compared to standard mechanical preparation
with a low residue diet.
We use artificial nutrition, with its associated morbidity and cost, as a therapeutic intervention to
accomplish some clinical objective. We should not think about it as “eating” or “feeding” (204),
particularly because these words have an inherent emotional value. It is appropriate to use RCTs to help
us make clinical decisions about employing, or not employing, these treatments.
A summary of the graded evidence of EN or VNS in the various disease states is presented in
Table 8. There is strong evidence for not using VNS in non-dysphagic stroke patients and for not
employing EN in the first week in patients who have strokes resulting in dysphagia. (It is likely, although
there is no evidence from RCTs, that, if the dysphagia persists for weeks, EN will ultimately be required.)
There is not quite strong evidence for providing VNS to malnourished geriatric patients. We were
unable to assign an A grade because the high quality trials did not show a statistically significant
improvement in survival. However, this was seen in the low quality trials and both high quality trials
found an effect in a favorable direction. A recent meta-analysis that was less restrictive in its definition of
supplements also found that oral supplements improved survival and reduced complication rates (205).
To be noted, these data cannot be extrapolated to healthy elderly individuals; there are no data for
providing dietary supplements to such people. Similarly, no data were identified to support the use of EN
in patients with end-stage dementia.
Data from low quality RCTs suggest that there is potential benefit for providing EN or VNS to
surgical patients who can tolerate these interventions or to patients with chronic liver disease. There was
similar low quality evidence for using EN as trophic feeding in low-birth-weight neonates or in critically
ill patients. However, the grades for the critically ill patients or those with chronic liver disease rest on
even more problematic data.
The grading in the critically ill is based on a study that was confounded by giving PN to some
control patients after 5 days (31); PN predisposes patients to infections (1). EN did not improve any
parameters of morbidity in patients with chronic liver disease, so it is unclear why it would improve
survival; furthermore, this significant difference in mortality was only demonstrable when the less
conservative model (fixed effects) was employed.
For the remaining disease states, there are no data to support the use of EN or VNS. Either there
were no (or an insufficient number of) RCTs available or the RCTs indicated that there was no benefit.
These data, as well as those for PN, are disappointing. Since malnutrition is accompanied by
adverse clinical consequences, why should its prevention or correction of malnutrition not improve
outcome? There are a number of possible reasons.
We may be providing the wrong formulations. Important nutrients may be absent, deficient, or
even excessive. However, since we do not know what to correct, we can only note that currently
available EN and VNS formulas lack established efficacy.
It does not appear to be a problem of inadequate delivery of artificial nutrition. The EN recipients
usually received more nutrients than did the controls; in only one RCT were the intakes comparable (20)
and no data were available in three others (33, 35, 36). We know that artificial nutrition does improve
nutritional outcomes (e.g. body weight or nitrogen balance), but improving these surrogate markers does
not translate into improved clinical outcome (206).
Many of the RCTs were small, and it would be unlikely that a limited benefit could be
demonstrated (perhaps even with data combination). We considered the problem of type II errors earlier.
Moreover, if only a small benefit exists, the clinician would have to weigh it against the resource
expenditures that would be required.
There may be patient subgroups for whom artificial nutrition would be beneficial; for example,
severely malnourished patients were usually excluded from the RCTs. However, if such subgroups do
exist, we have not yet identified them. Making a decision to treat everybody in order not to miss an
appropriate few will not accomplish any good.
There are shortcomings of the systematic review process. It may be that important RCTs were not
found. The search process did identify a large number of RCTs of artificial nutrition. Of course, if
investigators performing RCTs selectively avoided publishing the beneficial outcomes of the
interventions, the search process would have missed those data. However, the opposite phenomenon is
more likely to occur (207).
The methodologic quality of most of the studies included in this review was low. Some might
argue that we should disregard any data derived from such trials, as the data are unreliable. However,
since RCTs of low quality tend to produce an overestimation of a treatment benefit, a more realistic
concern is that the true treatment benefit is not as good as this current analysis has suggested.
Heterogeneity is always a problem in meta-analysis. We did limit these analyses to a similar
intervention in a similar disease state, and we also used statistical tests to decide which combining model
to employ. The random effects model, which tends to weigh smaller trials more heavily, could be
postulated to be susceptible to greater risk of bias, since small trials may be more influenced by bias. On
the other hand, the fixed effects model usually results in a smaller CI, so “significance” would be more
likely to be seen. In either event, with the single exception regarding the ability of EN to improve
survival in patients with chronic liver disease, no substantially different conclusions would have been
made if the alternative model was employed.
Finally, it may be that the interventions simply are not effective. The observed association
between malnutrition and poor outcome need not be causative; since sicker patients are likely to have
both, the malnutrition may only be an epiphenomenon. Also, while the duration of starvation or semi-
starvation that can be tolerated by a patient before the adverse effects of malnutrition occur is not clearly
defined, it is probably measured in weeks, not days.
Most of these observations were limited to patients who were not severely malnourished and who
would be without oral or enteral nutrients for no more than 14 days. There is no substantive information
from which to make conclusions about how or when to treat severely malnourished individuals or to
decide about the period of time beyond two weeks when it would be appropriate to employ artificial
nutrition. In such situations, or in those disease states for which data from RCTs are limited or non-
existent, the clinician will not have any evidence upon which to base a decision. Instead, he or she will
have to rely on an understanding of the patient’s clinical condition and anticipated outcome, a judgment
as to the patient’s ability to tolerate undernutrition, and an appreciation of the desires and needs of the
patient and his or her family.
For many of the clinical conditions, the evidence grades were based on a limited number of
studies. Future large trials could demonstrate effects that would change them. However, a
recommendation for implementation of this, or any other, therapy must be preceded by proof of efficacy.
The five authors performed this project without any external funding.
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