Somatostatin is an endogenous peptide that reduces splanchnic blood flow and gastrointestinal motility, inhibits acid secretion, and may have gastric cytoprotective effects [4-6]. Octreotide, a long-acting synthetic somatostatin analogue, has a similar activity profile [7]. Somatostatin is effective for controlling hemorrhage from esophageal varices [8, 9], but its efficacy for nonvariceal upper gastrointestinal hemorrhage is uncertain because randomized trials have had inconsistent results. This inconsistency may have been caused by small sample sizes and a resulting lack of power to detect differences or unstable estimates of differences; methodologic variation among the trials; or clinical heterogeneity of the study groups. In these circumstances, meta-analysis may be useful in reducing quantitative uncertainty, evaluating qualitative differences among trials, and suggesting reasons for inconsistent results. Therefore, we performed a meta-analysis of the published literature to determine the efficacy of somatostatin or octreotide compared with H₂ antagonists or placebo in the management of acute nonvariceal upper gastrointestinal hemorrhage.

Methods

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Study Identification and Selection

We searched the MEDLINE database from January 1966 to October 1996 and the EMBASE database from 1980 to October 1996 to identify all English-language literature included under the search headings somatostatin, octreotide, and gastrointestinal hemorrhage. We limited articles to human studies that were randomized, controlled trials or clinical trials. In addition, we performed an extensive manual search by using references from each retrieved report, review articles, and chapters from textbooks on gastroenterology.

To be included in our meta-analysis, studies had to be randomized clinical trials; had to include patients with acute nonvariceal upper gastrointestinal hemorrhage who had had confirmation of the source of bleeding by endoscopy; had to have compared somatostatin or octreotide with either an H₂ antagonist or placebo; and had to have used any combination of continuous or persistent bleeding, recurrent bleeding while receiving the intervention ("rebleeding on treatment"), need for surgery, or transfusion requirement as outcomes. We excluded articles that pertained to other research questions, review articles, editorials, and letters to the editor.

Qualitative Assessment

We independently evaluated the quality of trials with attention to the following methodologic standards for clinical trials [10]: 1) investigator blinding, 2) clearly defined inclusion and exclusion criteria, 3) baseline comparability of treatment and control groups, 4) standard and similar doses of the intervention agents, 5) clearly defined outcome variables, and 6) appropriate timing of the outcome in relation to treatment. We decided arbitrarily and a priori to consider the treatment and control groups to be similar at baseline if none of the baseline variables differed either statistically or clinically by 40% or more. We abstracted descriptive data to determine the extent to which the trials could be combined from a clinical perspective. After evaluation, we discussed differences and achieved consensus.

Empirical evidence suggests that poor concealment of allocation is associated with biased estimates of treatment effects. Therefore, although blinding of allocation was not examined initially, we examined the trials for this methodologic factor after analysis was completed [11].

Quantitative Assessment

After qualitative assessment, we independently extracted quantitative data from the trials. We did not attempt to contact the authors for missing information, nor were we blinded during quality assessment and data extraction. Numerical discrepancies were resolved by discussion. Because of the large number of trials, varying sample sizes, and differing clinical characteristics among study groups, we assumed that statistical heterogeneity was present, and we decided to use a random-effects model before combining the data. The random-effects model incorporates variability of results among trials and provides a more conservative estimate of an effect size by producing wider CIs [12, 13]. We used graphical displays of continued bleeding or rebleeding and the need for surgery [14] to help screen for heterogeneity. We tested our assumption by conducting a statistical test for homogeneity for each planned analysis by using the method of Der-Simonian and Laird [15], which is based on work first presented by Cochran [16].

We assumed that H₂ antagonists and placebo were equivalent as control interventions. We based this assumption on information in a report that contains data from 27 randomized trials, 20 of which compared H (₂) antagonists with placebo controls and suggested a 10% reduction at most in the risk for rebleeding with H₂ antagonists [17]. Therefore, in trials with more than one control (usually placebo and H₂ antagonist), the control groups were combined. The decision to combine control groups was a clinical one; it was made on the basis of these data and experts' evidence-based statements that H₂ antagonists do not alter the outcome of acute upper gastrointestinal hemorrhage [18].

Combining control groups in this way would tend to bias the analysis toward the null hypothesis because any efficacy of H₂ antagonists would reduce the effect size of somatostatin over placebo. To test the validity of the assumption that H₂ antagonists and placebo were therapeutically equivalent, we conducted preliminary analyses between somatostatin and each control group separately by using the pooled, unadjusted proportions of patients with continued bleeding or rebleeding. When stratified by control group, these proportions were 0.23 and 0.39 for the somatostatin and placebo groups, respectively, and 0.16 and 0.37 for the somatostatin and H₂ antagonist groups, respectively. The near equivalence of proportions for the two control groups supports our assumption.

For the initial analyses, we pooled all trials that measured a particular outcome and conducted subgroup analyses on the basis of predetermined criteria, such as exclusion of statistical outliers, investigator-blinded trials, and source of bleeding.

For all outcomes except transfusion requirement, the effect of treatment was computed by using pooled relative risks (RRs). Summary point estimates of effect were computed by using weighted averages of stratum-specific relative risks. The weights were derived from the reciprocals of the variances with an adjustment factor determined by the degree of statistical heterogeneity [19]. Thus, variation both within and among trials contributed to the variance estimates, resulting in wider confidence limits for more heterogeneous groups of trials. We calculated 95% CIs on the basis of the adjusted weights [20]. For relative risks that showed statistical significance (that is, if the 95% CI of the RR excludes 1), the number needed to treat (NNT) was calculated [21]. For this analysis, the NNT is the number of patients who need to be treated with somatostatin for one patient to derive additional benefit for a particular outcome over the benefit provided by H₂ antagonist or placebo. The NNT calculated by taking the reciprocal of the weighted difference in event rates between treatment and control groups. We calculated 95% CIs for the NNT by inverting the CIs for the absolute difference using the method of Fleiss [22]. These analyses and calculations were performed by using Supercalc spreadsheets (version 5.0, Computer Associates International, Inc., San Jose, California).

We calculated two numbers for mean transfusion requirement. The first was the effect size, which is the difference between the mean values for the control group (c) and the somatostatin group (ss) divided by the SD of the difference (s), or ([X_c – X_ss]/s). This number was weighted by trial sample size. Although the effect size is a standard measure for the meta-analysis of continuous variables, it has no units and does not translate easily into a clinically meaningful measure. Therefore, we calculated the difference in mean transfusion requirement weighted by the inverse of trial variance. We used SAS software (version 6.04, SAS Institute, Cary, North Carolina) for these calculations.

Results

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Descriptive and Qualitative Assessment

Searches of the MEDLINE and EMBASE databases yielded 50 references. Of these, 38 reports were excluded: Twenty-six were not pertinent to the research question (20 trials compared therapies for variceal bleeding, 4 compared different therapies for nonvariceal bleeding, and 2 were noncomparative studies), 7 were review articles, 2 were editorials, and 3 were letters to the editor. In addition to the 12 remaining pertinent references [23-34], 2 reports that fulfilled the inclusion criteria were found in a manual search [35, 36]. All reports were published as full-length papers; no abstracts were recovered.

Table 1 (and Table 5) shows descriptive clinical and methodologic characteristics of the 14 trials. In general, the study groups consisted of patients who were hospitalized for acute upper gastrointestinal hemorrhage of varying degrees of severity, as determined from clinical criteria. In all trials, upper endoscopy was done within 24 hours of admission to determine the source of bleeding. Exclusion criteria (which were not stated for 3 trials) varied somewhat but generally consisted of bleeding related to portal hypertension or cancer, presence of coagulopathy, renal insufficiency, pregnancy, or trivial or massive bleeding. The proportion of patients with active bleeding determined by endoscopy, reported in only 9 trials, ranged from 13% to 100% (Table 1 , Table 5).

Somatostatin was used in 12 trials at a standard dosage of 250 µg/h with or without a bolus dose; octreotide was used in 2 trials. Seven trials were placebo-controlled, 7 used cimetidine, and 5 used ranitidine. In 8 trials, the investigators were blinded to treatment assignment. Seven trials did not include enough detail to judge whether the allocation schedule had been adequately concealed. Six of the remaining 7 trials used adequate measures to conceal allocation according to published criteria [11].

Five trials had three treatment arms; four of these trials had placebo and H₂ antagonist control groups, and one had two different H (₂) antagonist control groups. For the most part, the treatment interval ranged from 48 to 72 hours but was as long as 120 hours. In 13 trials, the primary outcome variable was continued bleeding; this variable was defined by similar measures, including bloody nasogastric aspirate, vital signs, and need for transfusion during a specified time interval. In 8 of 13 trials, endoscopy was repeated to confirm evidence of continued bleeding. In the trial [28] that involved the most patients, the primary outcome was rebleeding, which was defined as fresh hematemesis or melena or an unexplained decrease in hematocrit in any 24-hour period after the first day. In this trial, the timing of rebleeding with respect to treatment was unclear; for our analysis, we assumed that all rebleeding occurred while patients were receiving treatment.

Table 2 contains numeric outcomes data and the authors' conclusions. The number of persons analyzed ranged from 20 to 534 and totaled 1829. The total study sample was 70% men, and the mean age of the sample was 64 years. Nine trials concluded that somatostatin was effective in some way over the comparison therapy; in three of these nine trials, the investigators were blinded to treatment assignment. Five trials, none of which had blinded investigators, concluded that there was no difference between somatostatin and H₂ antagonist or placebo. The two trials involving octreotide had sharply divergent conclusions: An investigator-blinded study concluded that octreotide had no effect on any outcome related to upper gastrointestinal bleeding [31], whereas a non-investigator-blinded study concluded that octreotide stopped peptic ulcer hemorrhage and decreased transfusion requirement, need for aggressive management (surgical or endoscopic intervention), and length of hospital stay [34].

Quantitative Assessment

Main Results

When all 1829 patients from the 14 trials were considered, somatostatin reduced the risk for continued bleeding or rebleeding to 0.53 (95% CI, 0.43 to 0.63), a risk reduction of 47% (Table 3). The NNT during the treatment period was 5 (CI, 3.2 to 9.1), meaning that 5 patients with acute nonvariceal upper gastrointestinal hemorrhage would need to be treated with somatostatin for up to 48 to 72 hours to prevent one case of continued bleeding or rebleeding. For the 12 trials that measured continued bleeding alone, the efficacy of somatostatin increased to a risk reduction of 56% (RR, 0.44 [CI, 0.33 to 0.55]; NNT, 5). Among 13 trials that measured the need for surgery, somatostatin reduced the risk to 0.71 (CI, 0.61 to 0.81; NNT, 8).

Figure 1 shows rates of continued bleeding or rebleeding during treatment in the treatment and control groups of individual trials. Most points lie above the diagonal line of unity and thus seem to favor somatostatin. Two potential outlier trials [26, 27] are indicated. The investigator-blinded trials are closer to the line of unity, indicating a more modest treatment effect. Figure 2 shows the rates of surgical intervention in the treatment and control groups, with potential outlier trials designated by arrows [27, 32]. Once again, the investigator-blinded trials indicate a more modest, if any, treatment effect.

View larger version (10K): [in this window] [in a new window]   Figure 1. Percentage of patients with continued bleeding or rebleeding during treatment in 14 randomized trials of somatostatin for treatment of nonvariceal upper gastrointestinal bleeding. The diagonal line represents the line of unity. Black squares indicate investigator-blinded trials; circles indicate trials in which investigators were not blinded; and arrows indicate statistical outliers [26, 27].

View larger version (10K): [in this window] [in a new window]   Figure 2. Percentage of patients who underwent surgery in the randomized trials of somatostatin for treatment of nonvariceal upper gastrointestinal bleeding. The diagonal line represents the line of unity. Black squares indicate investigator-blinded trials; circles indicate trials in which investigators were not blinded; and arrows indicate statistical outliers [27, 32].

In five trials [23, 29-31, 35], rebleeding during treatment was accurately determined among patients in whom bleeding had stopped. In an additional trial [28], the timing of rebleeding with respect to treatment could not be determined, nor were the numbers of patients in whom bleeding had stopped indicated. This trial was excluded from the analysis for rebleeding. Among the five trials, somatostatin showed no beneficial effect on rebleeding alone among patients in whom bleeding had stopped (RR, 1.09 [CI, 0.72 to 1.64]).

For continued bleeding or rebleeding and continued bleeding alone, exclusion of the trials that used octreotide had no substantial effect on the results (Table 3). It is important to note that in the overall analyses, P values for heterogeneity were statistically significant for all outcomes (P < 0.005), indicating greater-than-expected variation among results of the individual trials and implying that aggregating quantitative data may be problematic [14]. Exclusion of outlier trials had no notable effect on the results for continued bleeding or rebleeding and continued bleeding alone. For surgery, however, exclusion of the octreotide and outlier trials resulted in a statistically significant reduction in efficacy from a relative risk of 0.71 to a relative risk of 0.90 with nonoverlapping CIs (Table 3).

Among seven trials that provided enough information to measure the requirement for packed red blood cell transfusion (mean ±SD), the effect size weighted by trial sample size was 0.42 (CI, –0.10 to 0.93), indicating no statistical difference between the somatostatin and control groups. Although the weighted difference in transfusion requirement was 1.1 units less for somatostatin, the result was not statistically significant (CI, –0.6 to 2.8 units).

Five additional trials provided median or mean transfusion requirements without a variance measure (Table 2). In four of the five trials, the transfusion requirement was lower for patients receiving somatostatin or octreotide than for controls; in three of these four trials, the differences were statistically significant [33, 34, 36].

Subgroup Analyses

Subgroup analysis determines consistency of results and enumerates factors that may account for inconsistent results among individual trials. When we analyzed the subgroup of investigator-blinded trials, somatostatin remained efficacious for continued bleeding alone and with rebleeding (although it was less efficacious for the latter) (Table 4).

Somatostatin or octreotide was more effective for peptic ulcer bleeding than for non-peptic ulcer bleeding (which was mostly caused by hemorrhagic gastritis). Among 1178 patients from eight trials, somatostatin reduced the risk for continued bleeding or rebleeding from peptic ulcer to 0.48 (CI, 0.39 to 0.59; NNT, 4). For non-peptic ulcer bleeding, we saw a trend toward a decrease in risk for continued bleeding (RR, 0.62 [CI, 0.39 to 1.002]) (Table 4).

For the investigator-blinded subgroup of trials that examined the need for surgery, somatostatin or octreotide showed a trend toward efficacy (RR, 0.94 [CI, 0.87 to 1.001]) but was less efficacious than in the overall results.

With the exception of the subgroup based on peptic ulcer bleeding, the P values for heterogeneity were not statistically significant (range of P values, 0.09 to 0.25), indicating that aggregating the remaining subgroups shown in Table 4 is legitimate from a statistical perspective.

Discussion

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Because somatostatin inhibits several physiologic functions in the gastrointestinal tract, this agent and its analogues have been viewed as potentially useful for the treatment of several gastrointestinal diseases. Our meta-analysis examined 14 randomized clinical trials in which generic somatostatin or its long-acting analogue octreotide was used to treat nonvariceal upper gastrointestinal hemorrhage. Such qualitative and quantitative evaluation helps to estimate more precisely the effect of somatostatin on continued bleeding, need for surgery, and transfusion requirement. It also helps elucidate reasons for inconsistent results among the individual trials.

Although our overall results suggest that somatostatin or octreotide significantly reduces the risk for continued bleeding and the need for surgery, these results were derived from heterogeneous studies. More important and clinically applicable results came from the subgroup analyses. Among the subgroup of investigator-blinded trials, the efficacy of somatostatin for continued bleeding was more modest (although it remained clinically important and statistically significant); however, the need for surgery did not differ statistically between the somatostatin group and the control group. When stratified by underlying lesion, the effectiveness of somatostatin was limited to peptic ulcer bleeding, although a trend for non-peptic ulcer causes of bleeding was shown. Finally, the difference in the requirement for packed red blood cells was not statistically significant, although we saw a trend in favor of somatostatin. The sample size of eight studies had limited power to detect a clinically important difference.

Our analysis had some limitations. In the largest trial [28], the main outcome measure was rebleeding rather than continued bleeding. A shortcoming of this trial was that the timing of rebleeding with respect to treatment was unclear. For our meta-analysis, we assumed that rebleeding occurred during the 72-hour treatment period; however, rebleeding could have occurred at any time during the hospitalization. The main potential effect of including this trial (which had the most patients) was to bias the analysis in favor of no difference between the somatostatin and control groups: This largest trial showed no difference in rates of rebleeding and need for surgery.

An important criticism of meta-analysis is publication bias [37], in which studies that show statistically significant differences are published preferentially over studies that show no differences. Our electronic search strategy identified all but two trials, all of which were published as full-length reports. No abstracts were identified, and we could not find non-English language trials in a subsequent electronic search. We believe that all published reports were retrieved because we supplemented our electronic search with a rigorous manual search. Moreover, whether unpublished studies should be included in a meta-analysis is controversial. To determine the possible effects of publication bias, we calculated the number of unpublished trials showing no difference that would be required to nullify the efficacy of somatostatin for the outcome of continued bleeding or rebleeding during treatment among the investigator-blinded subgroup of eight trials. Known as the "file drawer effect" [37], the number of negative unpublished trials that would be required to bring the P value to 0.05 or greater is 18. Thus, we believe that publication bias was unlikely.

A limitation that is more important and more difficult to address is the extent to which the trials can be combined. Statistical heterogeneity among trials, a closely related issue, signifies greater-than-expected variability in the results of individual trials and suggests that aggregating the quantitative results may be ill advised [14]. However, meta-analysts disagree about this issue: Some regard heterogeneity as an opportunity to understand the reasons for divergent findings by exploring sources of heterogeneity [38-40]. The principal sources are variations in study protocols, outcome measures, interventions or cointerventions, and study groups. We consider each in turn.

All four of our main analyses showed heterogeneity (Table 3). However, subgroup analyses of investigator-blinded study protocols eliminated heterogeneity, suggesting that this factor may contribute to the discrepant results among individual trials. In contrast, the main outcome measures (continued bleeding or rebleeding during treatment and need for surgery) were similar from study to study and, we suspect, contributed little to trial heterogeneity.

It is also unlikely that differences in the interventions among the trials contributed substantially to heterogeneity. Although the dose of somatostatin was consistent among the trials, the duration of infusion ranged from 48 to 120 hours both within and among the trials. Because previous placebo-controlled trials of H₂ antagonists for treatment of acute upper gastrointestinal hemorrhage showed no clinically or statistically significant differences (and our preliminary analyses supported this result), we assumed that H₂ antagonists and placebo were therapeutically equivalent.

Study groups are yet another important source of heterogeneity. Although exclusion criteria were specific and consistent by comparison, broad and nonspecific inclusion criteria allowed for a spectrum of bleeding severity. An indicator of this breadth was the proportion of patients with active bleeding, which ranged from 13% to 100%. This variability does not include other important clinical factors that relate to outcome, such as rate of bleeding, amount of blood loss, presence of comorbid conditions, and existence of underlying lesion. These factors are plausible reasons for variability in the rates of continued bleeding among the control groups, which ranged from 15% to 90%. Stratification and analysis by underlying lesion reduced or eliminated heterogeneity; however, adjustment for other determinants of outcome was not possible because the data from the trials were available only at a summary level.

Thus, although heterogeneity obscures the clinical applicability of the pooled risk ratios in the main analyses, subgroup analyses indicate that intravenous somatostatin reduces the risk for persistent acute nonvariceal upper gastrointestinal hemorrhage caused by peptic ulcer disease and suggests that it may have a therapeutic role in the initial management of this clinical problem. By slowing or halting bleeding, somatostatin may be useful in the resuscitative phase of management and in enhancing the clinical utility of endoscopy by improving visualization of lesions. It might also have a role as an alternative therapy when endoscopy is unsuccessful, contraindicated, or unavailable. Our analysis highlights the need for further clarification of the effect of somatostatin in clinically distinct patient subgroups. This need could be met either with an individual patient-level analysis from these trials (provided that sufficient and similarly detailed data existed) or with a large clinical trial of somatostatin in patients who are carefully stratified or analyzed by source, severity, and type of bleeding.

Presented at the 50th Annual Meeting of the American College of Gastroenterology, 17 October 1995, New York, New York, and at the 17th Annual Meeting of the Society for Medical Decision Making, 17 October 1995, Tempe, Arizona.

Dr. Birgisson: Fagrihvammur, 810 Hveragerdi, Iceland.