A Systematic Review and Meta-Analysis on the Role of Somatostatin Therapy in Non-Variceal Gastrointestinal Bleeding

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

This systematic review and meta-analysis address a relevant clinical question regarding the utility of adjunctive somatostatin or its analogues in addition to proton-pump inhibitor (PPI) therapy for non-variceal upper gastrointestinal bleeding (NVUGIB). The authors followed standard systematic review methodology (PRISMA, PROSPERO registration) and performed meta-analyses for key clinical outcomes. The conclusion that adjunctive therapy does not offer significant benefits over PPI monotherapy for the outcomes studied is potentially important. However, the manuscript have several critical reporting errors, particularly concerning statistical results and their interpretation, and has some methodological limitations that need clarification and better discussion.

1. Title: the title has a strong decision on that Somatostatin Therapy Offers No Benefits in NVUGIB, although this is a systematic review. Therefore, the title should be changed into more convenient one such as “A Systematic Review and Meta-Analysis on the role of Somatostatin Therapy in Non-Variceal Gastrointestinal Bleeding”
2. Abstract: Line 23-24 (Mortality): Reports RR of 0.11 (95% CI, -0.69 to 0.91). Risk ratios cannot be negative, and their CIs must consist of non-negative values. This suggests a potential error in back-transforming from the log scale or a simple reporting mistake. The Results text (Line 182-183) reports the log RR as 0.11 (95% CI, -0.69 to 0.79), which is statistically plausible and consistent with the non-significant p-value (P=0.79) as the CI contains 0. The Abstract needs correction.
3. Abstract: Line 24-25 (Re-bleeding): Reports pooled RR of 1.04 (95% CI, 0.73 to -1.48). Again, a negative upper bound for an RR CI is impossible. The Results text (Line 190-191) states the pooled log RR was 1.04 (95% CI, 0.73-1.49; P=0.83). This CI [0.73, 1.49] for the log RR does not contain 0, which contradicts the reported P=0.83 (non-significant). Furthermore, Figure 3 (Forest plot for rebleeding) visually suggests an RR estimate close to 1 (log RR close to 0). It is highly likely the text intended to report the RR as 1.04, with a CI like [0.73, 1.49]. This CI does contain 1, consistent with P=0.83. These reporting errors are critical and must be corrected throughout the manuscript (Abstract, Results text, potentially Figures/Tables if affected). Ensure clarity and consistency between log RR and RR reporting and their respective CIs.
4. Results: Line 183-184: The text states "The use of PPI and PPI with adjunctive medical therapy was protective in nature with a risk reduction of 99.9%." This is a significant misinterpretation. The pooled log RR was 0.11 (95% CI -0.69 to 0.79), which corresponds to an RR of exp(0.11) ≈ 1.12 (95% CI exp(-0.69) to exp(0.79) ≈ 0.50 to 2.20). This result is non-significant (P=0.79) and the point estimate slightly favors higher (not lower) mortality risk with adjunctive therapy, although the CI is very wide and includes potential benefit and harm. There is absolutely no basis for claiming a 99.9% risk reduction. This sentence must be removed or drastically corrected to accurately reflect the non-significant finding and the calculated effect size and CI.
5. The reported search strategy (Line 72-73 and Table A1) uses keywords "upper gastrointestinal bleeding", "nonvariceal", and "somatostatin". This seems potentially restrictive. Were synonyms (e.g., UGIB, NVUGIB), related terms (e.g., peptic ulcer bleeding), or specific drug names (e.g., octreotide, vapreotide, lanreotide) included? Was a combination of keywords and database-specific subject headings (e.g., MeSH) used?. Please provide the full, detailed search strategy for at least one database (as recommended by PRISMA) in Appendix A, including all terms, Boolean operators, and any limits/filters applied. Clarify if specific drug names were searched.
6. The secondary outcome related to blood transfusion is described as "amount of blood transfusion" (Line 130, Line 229) but the analysis reported (Line 208-210, Figure 5B) seems to be a standardized mean difference (SMD) or similar, with a pooled estimate (-0.05) and CI identical to that reported for length of stay difference (Figure 4B). The legend for Figure 5B refers to "need for blood transfusion". Please clarify precisely what was measured (e.g., mean units transfused, proportion requiring any transfusion) and what effect measure was calculated and pooled (e.g., Mean Difference, SMD, RR, OR). Ensure consistency between text, figure labels, and analysis.
7. Statistical Methods: Line 144-145: Mentions using "95% Clopper-Pearson exact confidence intervals". This method is typically used for single binomial proportions. How was it applied to calculate CIs for pooled RRs, RDs, or SMDs from a meta-analysis? Standard methods (e.g., Wald-type on the log/logit scale, profile likelihood) are more common. Please clarify or correct.
8. Line 216: Mentions "dog plot" - assuming this is a typo for "doi plot" (as shown in Figure A1). Please correct.
9. Page 9, Lines 220, 221, 222 (Publication Bias): Mentions "Rita et al." three times. The study included in Table 1 and discussed elsewhere (e.g., Figure 2) appears to be "Riha et al., 2019". Please verify if "Rita" is a typo and should be "Riha".

 

Author Response

Please see the attachment and below.

Reviewer 1 comments:

“This systematic review and meta-analysis address a relevant clinical question regarding the utility of adjunctive somatostatin or its analogues in addition to proton-pump inhibitor (PPI) therapy for non-variceal upper gastrointestinal bleeding (NVUGIB). The authors followed standard systematic review methodology (PRISMA, PROSPERO registration) and performed meta-analyses for key clinical outcomes. The conclusion that adjunctive therapy does not offer significant benefits over PPI monotherapy for the outcomes studied is potentially important.”

1. “Title: the title has a strong decision on that Somatostatin Therapy Offers No Benefits in NVUGIB, although this is a systematic review. Therefore, the title should be changed into more convenient one such as “A Systematic Review and Meta-Analysis on the role of Somatostatin Therapy in Non-Variceal Gastrointestinal Bleeding.”

Authors’ response: Thank you for your insightful feedback regarding the manuscript title. We agree that the original title may imply a definitive conclusion that could be misinterpreted given the nature of a systematic review. In accordance with your suggestion, we have revised the title to: “A Systematic Review and Meta-Analysis on the Role of Somatostatin Therapy in Non-Variceal Gastrointestinal Bleeding” as shown in line 2-3 in the manuscript. This updated title provides a more neutral and balanced representation of the review content and aligns better with the standards expected of systematic reviews.

2. “Abstract: Line 23-24 (Mortality): Reports RR of 0.11 (95% CI, -0.69 to 0.91). Risk ratios cannot be negative, and their CIs must consist of non-negative values. This suggests a potential error in back-transforming from the log scale or a simple reporting mistake. The Results text (Line 182-183) reports the log RR as 0.11 (95% CI, -0.69 to 0.79), which is statistically plausible and consistent with the non-significant p-value (P=0.79) as the CI contains 0. The Abstract needs correction.”

Authors’ response: Thank you for pointing out the error in the originally reported risk ratio (RR) and confidence interval (CI) in the Abstract. You are absolutely correct that risk ratios cannot have negative confidence intervals. The originally reported value of “RR = 0.11 (95% CI, -0.69 to 0.91)” was mistakenly reported and, in fact, referred to a log-transformed risk ratio (log RR). In response to your helpful feedback, we have revised the Abstract and Results to remove log-transformed values and report only risk ratios (RR) and their corresponding 95% confidence intervals. This adjustment was made to improve clarity and clinical interpretability of our findings. The revised sentence now reads: “...the pooled risk ratio was 1.11 (95% CI, 0.50-2.48; P=0.79).” (line 23-24)

We also updated the relevant figures and their legends to reflect that all effect sizes are now presented on the risk ratio scale, with no log-transformed values reported. We believe this revision improves transparency and reader accessibility, and we appreciate your careful review, which prompted this important clarification.

3. “Abstract: Line 24-25 (Re-bleeding): Reports pooled RR of 1.04 (95% CI, 0.73 to -1.48). Again, a negative upper bound for an RR CI is impossible. The Results text (Line 190-191) states the pooled log RR was 1.04 (95% CI, 0.73-1.49; P=0.83). This CI [0.73, 1.49] for the log RR does not contain 0, which contradicts the reported P=0.83 (non-significant).

Authors’ response: Thank you for your careful attention to the reporting of our confidence intervals. We appreciate your observation regarding the value reported in the Abstract as “RR = 1.04 (95% CI, 0.73 to -1.48),” which understandably suggested an impossible negative upper bound. Upon review, we confirmed that the issue was a typographical formatting error, the hyphen between “0.73” and “1.48” was mistakenly interpreted as a negative sign rather than a range separator. The correct value is:

“RR = 1.04 (95% CI, 0.73-1.48; P=0.83).”

We have corrected this formatting in the revised Abstract (line 25) to avoid further misinterpretation.

Additionally, we acknowledge the concern regarding the discrepancy between the reported log RR and the p-value. After verifying the analysis output, we found that the original text erroneously labeled the result as a log RR, when in fact it was already the risk ratio (RR) on the natural scale. This has also been corrected throughout the manuscript to maintain consistency and accuracy. We thank you again for your thoughtful review and for helping us clarify these important details.

4. “Furthermore, Figure 3 (Forest plot for rebleeding) visually suggests an RR estimate close to 1 (log RR close to 0). It is highly likely the text intended to report the RR as 1.04, with a CI like [0.73, 1.49]. This CI does contain 1, consistent with P=0.83. These reporting errors are critical and must be corrected throughout the manuscript (Abstract, Results text, potentially Figures/Tables if affected). Ensure clarity and consistency between log RR and RR reporting and their respective CIs.”

Authors’ response: Thank you for this important observation regarding Figure 3 and the corresponding text in the Abstract and Results section. You are correct that the forest plot for rebleeding visually suggests a risk ratio (RR) close to 1, and not a log-transformed value. Upon reviewing the manuscript and original statistical outputs, we confirmed that the reported value of 1.04 with a 95% CI of [0.73, 1.49] reflects the risk ratio (RR), not the log risk ratio (log RR) as it was mistakenly labeled in some parts of the text.

To address this, we have:

• Corrected all mentions of “log RR” to “RR” where the values reported are on the original (natural) scale.
• Standardized the reporting format throughout the Abstract, Results, Tables, and Figures to consistently present RR and 95% CIs on the same scale.
• Updated the legend for Figure 3 to clearly indicate that the estimates shown are risk ratios, with the vertical line at RR = 1 representing the null effect.

These corrections ensure alignment between the statistical outputs, narrative interpretation, and figure presentation. We appreciate your close attention to detail and believe these updates improve the clarity and scientific integrity of the manuscript.

5. “Results: Line 183-184: The text states "The use of PPI and PPI with adjunctive medical therapy was protective in nature with a risk reduction of 99.9%." This is a significant misinterpretation. The pooled log RR was 0.11 (95% CI -0.69 to 0.79), which corresponds to an RR of exp(0.11) ≈ 1.12 (95% CI exp(-0.69) to exp(0.79) ≈ 0.50 to 2.20). This result is non-significant (P=0.79) and the point estimate slightly favors higher (not lower) mortality risk with adjunctive therapy, although the CI is very wide and includes potential benefit and harm. There is absolutely no basis for claiming a 99.9% risk reduction. This sentence must be removed or drastically corrected to accurately reflect the non-significant finding and the calculated effect size and CI.”

Authors’ response: Thank you for identifying this important discrepancy in our Results section. You are absolutely correct that the previously stated "risk reduction of 99.9%" is both misleading and inconsistent with the calculated effect size and confidence interval. Upon review, we recognized that this sentence stemmed from an earlier draft where we explored using risk difference as the effect size metric. The language of “risk reduction” aligns conceptually with absolute risk difference, not with risk ratios (RR), which were ultimately used in our final analysis and are now reported consistently throughout the manuscript. As you noted, our pooled estimate for mortality is RR=1.11 (95% CI, 0.50-2.48; P=0.79), which indicates no statistically significant difference and, in fact, suggests a slightly increased, not decreased, risk in the adjunctive therapy group. We inadvertently failed to remove the sentence referencing “99.9% risk reduction” during our transition to using RR as the primary effect size. In response to your comment, we have removed the incorrect sentence and carefully reviewed the manuscript to ensure all interpretations align accurately with the risk ratio framework. We appreciate your attention to this and believe this correction strengthens the scientific rigor of our reporting.

6. “The reported search strategy (Line 72-73 and Table A1) uses keywords "upper gastrointestinal bleeding", "nonvariceal", and "somatostatin". This seems potentially restictive. Were synonyms (e.g., UGIB, NVUGIB), related terms (e.g., peptic ulcer bleeding), or specific drug names (e.g., octreotide, vapreotide, lanreotide) included? Was a combination of keywords and database-specific subject headings (e.g., MeSH) used? Please provide the full, detailed search strategy for at least one database (as recommended by PRISMA) in Appendix A, including all terms, Boolean operators, and any limits/filters applied. Clarify if specific drug names were searched.”

Authors’ response: Thank you for your time and feedback. We have addressed this comment by adding the full detailed search strategy for the databases used (as recommended by PRISMA) in Appendix A (line 504-506) and specified in the text (line 75).

7. “The secondary outcome related to blood transfusion is described as "amount of blood transfusion" (Line 130, Line 229) but the analysis reported (Line 208-210, Figure 5B) seems to be a standardized mean difference (SMD) or similar, with a pooled estimate (-0.05) and CI identical to that reported for length of stay difference (Figure 4B). The legend for Figure 5B refers to "need for blood transfusion". Please clarify precisely what was measured (e.g., mean units transfused, proportion requiring any transfusion) and what effect measure was calculated and pooled (e.g., Mean Difference, SMD, RR, OR). Ensure consistency between text, figure labels, and analysis.”

Authors’ response: Thank you for your comment regarding the blood transfusion outcome. To clarify, the outcome measured was the mean amount of blood transfused per patient, as reported in the included studies. Due to variation in reporting units across studies, we used the standardized mean difference (SMD) as the pooled effect size. We have updated the manuscript to consistently describe this outcome as “amount of blood transfusion” and have revised the figure legend for Figure 5B (now renumbered as Figure 7) to reflect that the analysis presents a standardized mean difference (line 221-223). These changes have been incorporated for clarity and consistency.

8. “Statistical Methods: Line 144-145: Mentions using "95% Clopper-Pearson exact confidence intevals". This method is typically used for single binomial proportions. How was it applied to calculate CIs for pooled RRs, RDs, or SMDs from a meta-analysis? Standard methods (e.g., Wald-type on the log/logit scale, profile likelihood) are more common. Please clarify or correct.”

Authors’ response: Thank you for your thoughtful comment regarding the statistical methods. You are correct that Clopper-Pearson exact confidence intervals are most appropriate for estimating uncertainty around a single binomial proportion, and not typically used for pooled effect sizes such as risk ratios (RR), risk differences (RD), or standardized mean differences (SMD). In our analysis, the Clopper-Pearson method was used only for calculating 95% confidence intervals around the overall proportions (e.g., overall rebleeding or mortality rates), not for pooled comparisons or between-group effect estimates. For those pooled effect sizes, we employed standard meta-analytic techniques such as Wald-type confidence intervals. We have revised the Methods section to clarify this distinction and avoid confusion (lines 139-141). We appreciate your careful review and helpful suggestion, which has improved the transparency of our reporting.

9. “Line 216: Mentions "dog plot" - assuming this is a typo for "doi plot" (as shown in Figure A1). Please correct.”

Authors’ response: Thank you for your time and feedback. We have addressed this concern (line 137).

10. “Page 9, Lines 220, 221, 222 (Publication Bias): Mentions "Rita et al." three times. The study included in Table 1 and discussed elsewhere (e.g., Figure 2) appears to be "Riha et al., 2019". Please verify if "Rita" is a typo and should be "Riha".”

Authors’ response: Thank you. The typo has been checked and corrected throughout the manuscript.

Reviewer 2 Report

Comments and Suggestions for Authors

I would like to congratulate the authors for their effort in addressing an interesting and debated subject. Some thoughts and considerations are given below to help improve the manuscript primarily from the viewpoint of an endoscopist.

Minor considerations:

• The main causes for NVUGB are listed as gastric ulcers, duodenal ulcers and unknown etiology. However, angiodysplasias have been treated with somatostatin analogues with some promising results. It would be interesting if at least this category could be separately analyzed in the metanalysis. If not possible, it may be useful to perform sub-analyses for peptic ulcer disease alone (stated as 50% of cases included in the analysis) and excluding peptic ulcer disease (e.g. all other causes), using the same outcomes as for the overall analysis. This may help draw conclusions for more niche etiologies.

 

• It would be interesting to list the type (endoscopic, radiologic or both) and number of hemostatic procedures performed during hospital stay, as it may be that groups showed significant differences in this metric. Although it is stated that patients received endoscopic evaluation within 48h from admission, this does not clarify if hemostasis was obtained by endoscopic intervention or other invasive procedures or by pharmacological means only. By measuring the overall outcome only (e.g. mortality or need for surgery) it is practically impossible to deduce the actual efficacy of the two types of treatment. The efficacy comparison of the two drug regimens is actually highly dependent on the type of bleeding lesion, bleeding severity and type of endoscopic hemostasis performed , if any. If invasive hemostatic interventions were less needed in one group, this would clearly be an important indicator of actual treatment efficacy and could guide clinical decisions. As the paper stands the only pieces of data that could imply a potentially similar need for invasive hemostatic techniques in the 2 groups, thus confirming a similar efficacy of pharmacologic treatments) are:
  • the similar risk for need for surgery, a parameter which implies at least one previous failed non-surgical intervention but depends on the type and severity of individual cases
  • the similar duration of hospital stay, as a greater need for invasive procedures would probably necessitate longer stays; however this is also dependent on the initial severity of the case and the type of invasive hemostatic intervention performed at admission, if any.

 

I would suggest that, if available, invasive treatments performed be listed as number and percentage in each group. I would consider also performing a sub-analysis based on presence or absence of endoscopic intervention, especially the latter, if feasible.

Some of these considerations are already addressed in Discussion; however, the relevant section should be expanded to discuss more thoroughly the impact of endoscopic hemostasis or absence thereof in understanding and applying the conclusions of this metanalysis.

Figure 2 could be easier to interpret by the reader if the phrase “favors PPI monotherapy” and “favors PPI with adjunct medical therapy” were indicated along the x-axis. Similarly for figures 3-5.

Some minor revisions in the text, e.g. dashes not needed in lines 29, 31, 38, 39, repetition of the phrase “have been published” lines 62-63, “Further” instead of “Furthermore” in line 313, etc.

On Table B6, are Pooled Effect Sizes expressed as odd ratios?

Author Response

Reviewer 2 comments:

1. “I would like to congratulate the authors for their effort in addressing an interesting and debated subject. Some thoughts and considerations are given below to help improve the manuscript primarily from the viewpoint of an endoscopist.”

Authors’ response: We sincerely thank the reviewer for their kind words and thoughtful review of our manuscript. We appreciate your recognition of the importance of this debated topic and your insights from the perspective of an endoscopist. Your comments have helped us enhance the clarity, transparency, and methodological rigor of our work. Below, we provide detailed responses and revisions made in response to your specific suggestions.

2. “The main causes for NVUGB are listed as gastric ulcers, duodenal ulcers and unknown etiology. However, angiodysplasias have been treated with somatostatin analogues with some promising results. It would be interesting if at least this category could be separately analyzed in the metanalysis. If not possible, it may be useful to perform sub-analyses for peptic ulcer disease alone (stated as 50% of cases included in the analysis) and excluding peptic ulcer disease (e.g. all other causes), using the same outcomes as for the overall analysis. This may help draw conclusions for more niche etiologies.”

Authors’ response: We thank the reviewer for highlighting the importance of stratifying NVUGIB etiologies, particularly the potential differential effect of somatostatin analogs in patients with angiodysplasias. We agree that angiodysplasias represent a mechanistically distinct cause of bleeding and may respond differently to pharmacologic therapy. Unfortunately, most of the included studies did not provide granular data allowing for separate analysis of angiodysplasia-related bleeds. Similarly, while peptic ulcer disease was the most commonly reported etiology (approximately 50% of cases), data were insufficiently detailed across studies to perform reliable subgroup analyses comparing peptic ulcer vs. non-peptic ulcer causes. We have added this limitation to the Discussion section (line 391-400) and emphasized the need for future studies to better classify and report etiology-specific data to enable such subgroup analyses.

Added in the Discussion:

“In addition, the included studies varied in how they reported the underlying causes of NVUGIB. While peptic ulcer disease accounted for approximately 50% of patients, other etiologies such as angiodysplasias were either grouped into broader categories or not separately reported. Given that somatostatin analogs may have particular benefit in vascular lesions such as angiodysplasias, this lack of etiological specificity limited our ability to conduct meaningful subgroup analyses. Separate analysis of peptic ulcer-related bleeding versus non-ulcer etiologies (including angiodysplasia) was not feasible due to insufficiently stratified data across studies. Therefore, future trials and meta-analyses to clearly report and analyze outcomes by etiology to better understand the potential role of somatostatin therapy across distinct NVUGIB subtypes are recommended.”

3. “It would be interesting to list the type (endoscopic, radiologic or both) and number of hemostatic procedures performed during hospital stay, as it may be that groups showed significant differences in this metric. Although it is stated that patients received endoscopic evaluation within 48h from admission, this does not clarify if hemostasis was obtained by endoscopic intervention or other invasive procedures or by pharmacological means only. By measuring the overall outcome only (e.g. mortality or need for surgery) it is practically impossible to deduce the actual efficacy of the 2 types of treatment. The efficacy comparison of the 2 drug regimens is actually highly dependent on the type of bleeding lesion, bleeding severity and type of endoscopic hemostasis performed, if any. If invasive hemostatic interventions were less needed in one group, this would clearly be an important indicator of actual treatment efficacy and could guide clinical decisions. As the paper stands the only pieces of data that could imply a potentially similar need for invasive hemostatic techniques in the 2 groups, thus confirming a similar efficacy of pharmacologic treatments) are.

• the similar risk for need for surgery, a parameter which implies at least one previous failed non-surgical intervention but depends on the type and severity of individual cases
• the similar duration of hospital stays, as a greater need for invasive procedures would probably necessitate longer stays; however, this is also dependent on the initial severity of the case and the type of invasive hemostatic intervention performed at admission, if any.”

Authors’ response: We thank the reviewer for this helpful comment. We have included this information as an extra column (column 3 from the left) in Table 2 (line 171).

4. “I would suggest that, if available, invasive treatments performed be listed as number and percentage in each group. I would consider also performing a sub-analysis based on presence or absence of endoscopic intervention, especially the latter, if feasible.”

Authors’ response: Thank you for your very helpful comment. Although 3 of our included studies did include the number of patients undergoing invasive treatments in both the PPI monotherapy and PPI with octreotide therapy groups, they did not provide the primary and secondary outcomes based on whether patient underwent invasive treatments. In this way, sub-analysis based on presence or absence of endoscopic intervention on outcomes (i.e., mortality) was not feasible.

5. “Some of these considerations are already addressed in Discussion; however, the relevant section should be expanded to discuss more thoroughly the impact of endoscopic hemostasis or absence thereof in understanding and applying the conclusions of this metanalysis.”

Authors’ response: We thank the reviewer for highlighting the importance of analyzing the impact of endoscopic hemostasis or absence thereof in understanding and applying the conclusions of this metanalysis. We have included this discussion based on our results in the discussion section (lines 297-304).

Added in the Discussion:

“Our results show that there was no consistency regarding which group (PPI monotherapy compared to PPI with somatostatin and its analogs) had more patients undergoing invasive treatment with endoscopy after treatment was given. Although subgroup analysis was not feasible to give a definitive conclusion on the impact of endoscopic hemostasis in the context of our study, this finding may be a signaling result to consider that not giving somatostatin and its analogs does not predispose patients to increased risk for bleeding requiring endoscopic hemostasis.”

6. “Figure 2 could be easier to interpret by the reader if the phrase “favors PPI monotherapy” and “favors PPI with adjunct medical therapy” were indicated along the x-axis. Similarly, for figures 3-5.”

Authors’ response: Thank you for your time and feedback. We added this footnote to each figure for more clarity. For interpretability, the direction of effect is indicated along the x-axis: values to the left of the null line (RR = 1 or SMD = 0) favor PPI monotherapy, while values to the right favor PPI with adjunctive medical therapy.

7. “Some minor revisions in the text, e.g. dashes not needed in lines 29, 31, 38, 39, repetition of the phrase “have been published” lines 62-63, “Further” instead of “Furthermore” in line 313, etc.”

Authors’ response: Thank you! The suggested corrections have been made.

8. “On Table B6, are Pooled Effect Sizes expressed as odd ratios?”

Authors’ response: Thanks for your question. These are expressed as pooled risk ratios.

Reviewer 3 Report

Comments and Suggestions for Authors

1) The included studies had different ways of giving the drugs, some gave PPI first, others gave somatostatin first, and some gave them far apart in time. Also, the dose and way of giving somatostatin (injection, infusion or different amounts) were not the same. This makes the results not easy to trust because we don’t know if differences in treatment made the results look better or worse than they really are. The authors should say clearly that this is a strong limitation.

2) The paper also did not report or adjust for how bad the bleeding was in each patient. Some patients had light bleeding and others maybe had very strong bleeding, but the study treated them all the same in the analysis. There was no Forrest classification or other clinical scale used to measure bleeding severity. This could hide a possible benefit of somatostatin in high-risk patients. The authors must say this in the discussion and not just in passing.

3) The authors did not use meta-regression which is very important in a meta-analysis when studies are so different. Meta-regression helps to see if dose, timing, or drug route change the results. Not using this tool is a missed chance to explain the results better. The authors should at least say they did not use it and that this weakens the statistical power. They also didn’t use the GRADE tool to show how strong or weak the evidence is. GRADE is expected in this kind of paper. The paper should explain why it was not used and say this is a limitation of the evidence certainty.

4) Another issue is the patient differences. Some had shock, some used blood thinners, some had H. pylori and some did not. These things can affect rebleeding or death. But the paper did not adjust for these things or try to control them. Also, it’s not clear how the patients were chosen for somatostatin or PPI alone. Maybe the doctors picked the sicker patients to get both drugs and this can confuse the results (selection bias). The authors must say this clearly as a possible source of bias.

5) Giving the drug early or late can change how well it works. But the study did not control when the drugs were given. Some studies gave the drugs before endoscopy and some after this. This makes it hard to compare outcomes. The authors should say in the discussion that drug timing is a problem and should be fixed in future studies.

6) As we know, somatostatin is expensive. If it gives no benefit, that is very important for hospitals and patients. The authors should talk about the cost and suggest doing cost-effectiveness studies next time. Also, they could have made a simple algorithm or flowchart to help doctors know when to use or not use somatostatin. That would help with real-world decisions, and increase the importance of this study to the medical community.

7) Some studies didn’t report all needed data. For example, adverse effects of somatostatin were not well shown. Even if they say there were no serious side effects, this is not enough. We need numbers, types of side effects and how many people had them. Without this, we can’t know if the drug is safe or not.

8) Some studies were retrospective and some were randomized trials. Mixing both types in a meta-analysis adds more noise. The authors used Cochrane and MINORS scores, which is good but they did not use subgroup analysis to compare results from stronger studies versus weaker ones. They must do this or say why they did not.

9) There is also no analysis based on ICU use or need for vasopressors, which could show different responses to treatment. Patients in shock or ICU may benefit more from somatostatin but this is not tested. This must be said in the limitations too.

10) The reporting bias is low according to funnel plots, but still one big study (Riha et al.) had high weight in the analysis. Even if sensitivity analysis shows little change, this dominance should be discussed more carefully, especially when the total number of studies is small.

11) The authors should say that their conclusion is limited by major variability in treatments, weak control of confounders and missing information. They should not say too strongly that PPI is always enough for all NVUGIB cases. Instead, they should say that more good-quality trials are needed at this moment, using fixed doses, fixed timing and proper patient selection.

Author Response

Reviewer 3 comments:

1. “The included studies had different ways of giving the drugs, some gave PPI first, others gave somatostatin first, and some gave them far apart in time. Also, the dose and way of giving somatostatin (injection, infusion or different amounts) were not the same. This makes the results not easy to trust because we don’t know if differences in treatment made the results look better or worse than they really are. The authors should say clearly that this is a strong limitation.”

Authors’ response: We thank the reviewer for this insightful and important observation. We fully agree that the variability in the administration of both PPI and somatostatin therapy across the included studies—including differences in the order of drug administration, dosing intervals, methods of delivery (e.g., infusion vs. injection), and timing relative to endoscopy—represents a significant source of clinical heterogeneity. These inconsistencies could have impacted the pooled effect estimates, either attenuating or exaggerating the observed outcomes.

In response to this comment, we have expanded the Limitations section of the Discussion to explicitly and more prominently identify this heterogeneity as a major limitation of our meta-analysis (lines 309-326). We now emphasize that the lack of standardization may compromise the interpretability of results and confound the true impact of adjunctive therapy. We also highlight the need for future studies using standardized protocols to better evaluate the role of somatostatin analogs in managing NVUGIB. We appreciate the reviewer’s suggestion, which has enhanced the clarity and rigor of our manuscript.

Revised Paragraph in the Discussion:

“However, there are notable limitations to our study, most importantly the substantial clinical heterogeneity in treatment methodology among the included trials. Specifically, the studies differed in the order in which PPI and somatostatin analogs were administered, the timing between doses, and the route and dosage of somatostatin (e.g., subcutaneous injection vs. intravenous infusion, standard vs. high doses). In several studies, the drugs were given hours apart or the sequence of administration was not clearly reported, which could impact drug synergy and clinical effectiveness. Additionally, the timing relative to endoscopy varied, with some patients receiving pharmacologic treatment before and others after the procedure. Such variability likely introduced confounding factors that may have influenced treatment outcomes, either underestimating or overestimating the efficacy of adjunctive therapy. This heterogeneity limits the strength and generalizability of our conclusions."

“Future research should implement standardized protocols for drug administration, dosing, and timing to enable more reliable assessments of the therapeutic value of somatostatin analogs in NVUGIB management.”

2. “The paper also did not report or adjust for how bad the bleeding was in each patient. Some patients had light bleeding and others maybe had very strong bleeding, but the study treated them all the same in the analysis. There was no Forrest classification or other clinical scale used to measure bleeding severity. This could hide a possible benefit of somatostatin in high-risk patients. The authors must say this in the discussion and not just in passing.”

Authors’ response: We thank the reviewer for this important observation. We agree that bleeding severity is a critical clinical factor that may influence both treatment response and outcomes. Unfortunately, most included studies did not report bleeding severity using standardized clinical tools, such as the Forrest classification, Rockall score, or other validated scales. As a result, we were unable to stratify or adjust our meta-analysis based on the severity of bleeding at presentation. We acknowledge that this limitation may have masked a potential benefit of adjunctive somatostatin therapy in high-risk or severely bleeding patients, as the pooled analysis treats all patients as a homogeneous population. In response, we have revised the Discussion to explicitly highlight this issue as a significant limitation and have emphasized the need for future studies to include and stratify by validated bleeding severity scores (lines 415-422).

Added in the Discussion:

“Also, most included studies did not report bleeding severity using standardized clinical tools, such as the Forrest classification, Rockall score, or other validated scales. As a result, we were unable to stratify or adjust our meta-analysis based on the severity of bleeding at presentation. This limitation may have masked a potential benefit of adjunctive somatostatin therapy in high-risk or severely bleeding patients, as the pooled analysis treats all patients as a homogeneous population. This highlights the need for future studies to include and stratify by validated bleeding severity scores.”

3. “The authors did not use meta-regression which is very important in a meta-analysis when studies are so different. Meta-regression helps to see if dose, timing, or drug route change the results. Not using this tool is a missed chance to explain the results better. The authors should at least say they did not use it and that this weakens the statistical power.

Authors’ response: Thank you for highlighting the absence of meta-regression. We agree that this analytical approach can be valuable in identifying whether differences in dosage, timing, or drug route influence outcomes. However, given that our meta-analysis included only 7 studies, we refrained from performing meta-regression due to concerns about statistical reliability and risk of spurious associations in small samples. As noted by Thompson and Higgins (2002), meta-regression should be interpreted with caution in datasets containing fewer than 10 studies, as the power to detect moderator effects is low and the likelihood of false-positive results is increased. We have added this rationale to the Discussion section and acknowledged this as a limitation and area for future study (lines 401-408).

Reference # 28:

Thompson SG, Higgins JP. How should meta‐regression analyses be undertaken and interpreted? Stat Med. 2002;21(11):1559–1573. DOI:10.1002/sim.1187

Added in the Limitations:

Next, another limitation is the absence of meta-regression, which could have explored whether differences in dosage, timing, or route of drug administration moderated the effects observed. Given the variability in intervention protocols among included studies, meta-regression would have added important nuance to understanding heterogeneity. However, due to the relatively small number of studies (n=7), we did not perform meta-regression, as its statistical power is limited in small samples and can yield unreliable or spurious associations. As noted by Thompson and Higgins, meta-regression should generally be avoided unless at least 10 studies are included in the analysis [28].

4. “They also didn’t use the GRADE tool to show how strong or weak the evidence is. GRADE is expected in this kind of paper. The paper should explain why it was not used and say this is a limitation of the evidence certainty.”

Authors’ response: We thank the reviewer for drawing attention to the absence of a formal GRADE assessment in our meta-analysis. While we recognize the value of the GRADE framework in systematically evaluating the certainty of evidence, we chose not to include it in this review for several justifiable reasons. First, the number of included studies (n=7) was relatively small, and as noted by the GRADE Working Group, applying GRADE in small meta-analyses may offer limited differentiation in certainty levels and reduced interpretability [Guyatt et al., 2008]. Second, several of the included studies lacked the detailed reporting necessary for a robust GRADE assessment, such as precise estimates of effect, standardized outcome reporting, or assessments of indirectness and imprecision making consistent application of GRADE criteria difficult and potentially subjective [Murad et al., 2014]. Instead, we relied on established methodological tools, such as the Cochrane RoB 2 for randomized trials and the MINORS instrument for non-randomized studies, which allowed us to transparently assess the internal validity and quality of the included studies. Nonetheless, we agree that the omission of GRADE is a limitation, as it restricts our ability to fully characterize the overall certainty of the evidence. We have now addressed this limitation in the revised Discussion section and have recommended that future meta-analyses incorporate the GRADE framework to enhance evidence synthesis and guideline development (lines 426-434).

References:

Guyatt GH, Oxman AD, Vist GE, et al. GRADE: an emerging consensus on rating quality of evidence and strength of recommendations. BMJ. 2008;336(7650):924–926. DOI:10.1136/bmj.39489.470347.AD

Murad MH, Montori VM, Ioannidis JPA, et al. How to read a systematic review and meta-analysis and apply the results to patient care: Users' guides to the medical literature. JAMA. 2014;312(2):171–179. DOI:10.1001/jama.2014.5559

Added in the Discussion:

“Another important limitation is the absence of a formal GRADE (Grading of Recommendations Assessment, Development, and Evaluation) assessment. Several included studies lacked adequate detail for assessing precision, consistency, and indirectness, which are the key domains within the GRADE framework making standardized grading difficult and potentially subjective [29,30]. Although we employed validated tools such as the Cochrane RoB 2 and MINORS to assess study quality, we acknowledge that the omission of GRADE limits our ability to fully communicate the overall certainty of the evidence. Therefore. future systematic reviews on this topic should consider incorporating both meta-regression and GRADE to enhance transparency and evidence synthesis.”

5. “Another issue is the patient differences. Some had shock, some used blood thinners, some had H. pylori and some did not. These things can affect rebleeding or death. But the paper did not adjust for these things or try to control them. Also, it’s not clear how the patients were chosen for somatostatin or PPI alone. Maybe the doctors picked the sicker patients to get both drugs and this can confuse the results (selection bias). The authors must say this clearly as a possible source of bias.”

Authors’ response: We thank the reviewer for highlighting this important concern. We agree that patient-level differences, such as hemodynamic instability (shock), anticoagulant use, and presence or absence of Helicobacter pylori infection, can significantly influence outcomes such as rebleeding and mortality. Unfortunately, the included studies did not provide sufficient data to allow for adjusted analyses or stratification by these variables. This is an acknowledged limitation that may have contributed to uncontrolled confounding in the pooled results. Additionally, we recognize the potential for selection bias, particularly in non-randomized studies where sicker patients may have been preferentially assigned to receive adjunctive somatostatin therapy. Since treatment allocation was not consistently randomized or clearly reported, it is possible that baseline differences between groups may have skewed the results. In response to the reviewer’s comment, we have revised the Discussion section to more explicitly describe these sources of bias and their implications for the validity of our findings (lines 339-351).

Added in the Discussion:

“Another key limitation is the potential for confounding by baseline patient characteristics. Across the included studies, patients varied significantly in clinical status: some presented with hemodynamic instability (shock), others were taking anticoagulants or antiplatelet agents, and some had confirmed H. pylori infection while others did not. These factors are known to influence outcomes such as rebleeding and mortality, but due to inconsistent or incomplete reporting, we were unable to perform adjusted analyses or stratify patients by these variables. As a result, our pooled estimates may reflect uncontrolled confounding. Moreover, in the non-randomized studies, treatment allocation was not clearly described, and it is possible that sicker patients were more likely to receive somatostatin along with PPI, introducing selection bias. This could artificially attenuate or exaggerate the observed effects of adjunctive therapy, limiting the internal validity of our findings, which highlights the need for future randomized studies with rigorous control for baseline confounders.”

6. “Giving the drug early or late can change how well it works. But the study did not control when the drugs were given. Some studies gave the drugs before endoscopy and some after this. This makes it hard to compare outcomes. The authors should say in the discussion that drug timing is a problem and should be fixed in future studies.”

Authors’ response: We thank the reviewer for this valuable comment. We agree that timing of drug administration, especially in relation to endoscopy is an important variable that can influence therapeutic effectiveness. In our meta-analysis, there was substantial variability in when PPIs and somatostatin analogs were administered, with some studies administering these drugs before endoscopy, while others administered them after. Unfortunately, this variability was not consistently documented or controlled across the included studies, which adds to the clinical heterogeneity and complicates interpretation of treatment effects. We have revised the Discussion section to highlight this as a critical limitation and emphasized the need for standardized timing protocols in future clinical trials to better assess the efficacy of adjunctive therapy in NVUGIB (lines 315-326).

Added in the Discussion:

“Timing of drug administration represents another important limitation of this study. Across the included trials, there was no consistent control over when PPIs and somatostatin analogs were initiated relative to diagnostic or therapeutic endoscopy. In some studies, the drugs were given prior to endoscopy, while in others, they were administered after the procedure. This inconsistency in timing is critical, as the effectiveness of acid suppression and vasoactive therapies is time-sensitive, earlier administration may enhance clot stability and reduce active bleeding. The inability to account for or standardize drug timing across studies contributes to methodological heterogeneity and may have obscured the true impact of adjunctive treatment. Future studies should incorporate uniform protocols specifying the timing of drug initiation, especially in relation to endoscopic evaluation, to allow for more accurate comparisons of clinical outcomes.”

7. “As we know, somatostatin is expensive. If it gives no benefit, that is very important for hospitals and patients. The authors should talk about the cost and suggest doing cost-effectiveness studies next time. Also, they could have made a simple algorithm or flowchart to help doctors know when to use or not use somatostatin. That would help with real-world decisions, and increase the importance of this study to the medical community.”

Authors’ response: We thank the reviewer for this thoughtful and practical recommendation. We agree that cost considerations are critical, particularly for therapies like somatostatin that are expensive and resource-intensive. Our findings of no statistically significant benefit with adjunctive somatostatin therapy highlight the potential cost burden without corresponding clinical gain, which is highly relevant for hospital formularies, clinical practice, and healthcare policy.

In response, we have revised the manuscript to underscore the need for future cost-effectiveness studies to evaluate whether the use of somatostatin in NVUGIB provides value relative to its cost. Additionally, we appreciate the reviewer’s suggestion to provide a clinical decision aid or algorithm. While our current review did not include enough consistent data to develop a robust algorithm, we acknowledge this as an important future direction and have noted this explicitly in the revised text (lines 448-457).

Added in the Conclusion:

“Somatostatin and its analogs are significantly more expensive than standard PPI therapy. Given our finding that adjunctive therapy offered no added clinical benefit, the financial implications are considerable for both healthcare institutions and patients. This underscores the need for future cost-effectiveness analyses to evaluate whether somatostatin use in NVUGIB is justified based on health outcomes and economic impact. Furthermore, we recognize the value of developing clinical decision algorithms or flowcharts to help guide the use of adjunctive therapy in real-world settings. While the current evidence is insufficient to construct such a tool with high confidence, this represents a meaningful area for future work that could improve clinical decision-making and optimize resource utilization.”

8. “Some studies didn’t report all needed data. For example, adverse effects of somatostatin were not well shown. Even if they say there were no serious side effects, this is not enough. We need numbers, types of side effects and how many people had them. Without this, we can’t know if the drug is safe or not.”

Authors’ response: We thank the reviewer for this crucial comment regarding the incomplete reporting of adverse effects. We agree that safety data is essential to fully assess the risk-benefit profile of any pharmacologic intervention, including somatostatin and its analogs. While several included studies stated that no serious adverse events were observed, most did not provide quantitative data on adverse events, including the type, frequency, and severity of side effects. We acknowledge that this lack of detailed reporting limits the ability to assess the safety of adjunctive therapy and may contribute to underestimating its risks. In response to the reviewer’s comment, we have revised the Discussion section to explicitly state this limitation and emphasize the importance of comprehensive safety reporting in future studies (lines 364-374).

Revised paragraph in the Discussion:

“A further limitation of our study is the incomplete reporting of adverse events related to somatostatin and its analogs in the included trials. Although some studies noted that no severe adverse events occurred, they generally did not provide detailed data on non-serious side effects such as gastrointestinal discomfort, bradycardia, cholelithiasis, or metabolic disturbances, which are known potential complications of somatostatin use. Without consistent and quantitative reporting of adverse events, including type, frequency, and severity, it is not possible to fully assess the safety profile of adjunctive therapy. This lack of data limits our ability to draw definitive conclusions about the risk-to-benefit ratio of somatostatin in NVUGIB. Future trials should include systematic adverse event monitoring and transparent reporting to better inform clinical risk assessments.”

9. “Some studies were retrospective and some were randomized trials. Mixing both types in a meta-analysis adds more noise. The authors used Cochrane and MINORS scores, which is good but they did not use subgroup analysis to compare results from stronger studies versus weaker ones. They must do this or say why they did not.”

Authors’ response: We thank the reviewer for this important observation. We agree that combining randomized controlled trials (RCTs) and retrospective observational studies in a meta-analysis can introduce methodological heterogeneity and potentially obscure differences in treatment effects. While we assessed the risk of bias using Cochrane criteria for RCTs and MINORS for non-randomized studies, we acknowledge that we did not conduct a formal subgroup analysis based on study design or quality. This decision was based on the limited number of total included studies (n=7), which constrained the feasibility and interpretability of subgroup comparisons. With such a small sample, stratifying by design would have yielded subgroups too small to generate reliable or statistically meaningful results. However, we now explicitly recognize this as a limitation in our analytic approach and note that future meta-analyses with a larger number of trials should include such subgroup comparisons to explore the impact of study design on effect estimates (lines 408-415).

Added in the Discussion:

“Additionally, we did not perform a subgroup analysis based on study design or methodological quality. This omission was due to the limited number of studies, which precluded meaningful statistical comparisons between design types. However, we recognize that mixing study designs may increase the risk of bias and heterogeneity in the pooled estimates. Future meta-analyses that include a greater number of studies should incorporate stratified analyses by study type to assess the robustness of findings and better understand how study design influences the observed outcomes.”

10. “There is also no analysis based on ICU use or need for vasopressors, which could show different responses to treatment. Patients in shock or ICU may benefit more from somatostatin but this is not tested. This must be said in the limitations too.”

Authors’ response: We thank the reviewer for raising this important point regarding the potential role of ICU status and vasopressor use in influencing treatment response. We agree that patients in critical care settings, particularly those in shock or requiring vasopressors, may exhibit different clinical trajectories and could potentially benefit more from somatostatin therapy due to its physiological effects on splanchnic circulation. Unfortunately, the included studies did not provide stratified or subgroup data based on ICU admission or vasopressor use, and therefore we were unable to analyze these potentially meaningful subpopulations. We have now acknowledged this limitation explicitly in the revised Discussion section and identified it as an important direction for future research to better understand treatment effects in more severely ill patients (lines 383-390).

Added in the Discussion:

“Additionally, none of the included studies reported outcomes stratified by ICU admission status or need for vasopressor support. These clinical indicators are important markers of illness severity and may modify the response to adjunctive therapy. It is plausible that patients in shock or those requiring intensive care support could benefit more from somatostatin-based therapy due to its effects on splanchnic blood flow and hemodynamic stability. However, without subgroup analysis based on ICU or vasopressor use, we were unable to explore this hypothesis. Authors acknowledge this as a further limitation and suggest it as a focus for future prospective studies.”

11. “The reporting bias is low according to funnel plots, but still one big study (Riha et al.) had high weight in the analysis. Even if sensitivity analysis shows little change, this dominance should be discussed more carefully, especially when the total number of studies is small.”

Authors’ response: Thank you. The suggested correction has been made (lines 266-273).

Added in the Discussion:

“It is important to note that in our analysis, one study contributed disproportionately to the overall effect size, accounting for nearly 50% of the weight in certain pooled outcomes due to its larger sample size. Although the leave-one-out sensitivity analysis showed minimal impact on overall estimates when this study was excluded, the limited number of studies in the meta-analysis amplifies the influence of any single study. Therefore, the dominance of one study must be interpreted with caution, as it could obscure or amplify treatment effects, and we consider this a notable limitation of the evidence synthesis.”

12. “The authors should say that their conclusion is limited by major variability in treatments, weak control of confounders and missing information. They should not say too strongly that PPI is always enough for all NVUGIB cases. Instead, they should say that better-quality trials are needed at this moment, using fixed doses, fixed timing and proper patient selection.”

Authors’ response: We appreciate the reviewer’s thoughtful comment on the strength and framing of our conclusions. We agree that the conclusion should reflect the limitations of the current evidence, including variability in treatment protocols, lack of consistent control for confounding factors, and incomplete clinical reporting across included studies. To address this, we have revised both the Abstract and the Conclusion section of the manuscript to clearly state that while our findings show no statistically significant benefit of adjunctive somatostatin therapy, this interpretation is limited by methodological inconsistencies and potential biases. Rather than suggesting that PPI monotherapy is universally sufficient for all NVUGIB cases, we now emphasize the need for better-quality randomized controlled trials using standardized doses, timing, and patient selection criteria. In addition, we have revised the manuscript’s title to a more neutral and methodologically appropriate version: “A Systematic Review and Meta-Analysis on the Role of Somatostatin Therapy in Non-Variceal Gastrointestinal Bleeding.” (lines 28-35 and lines 436-457) This revised title better reflects the nature of a systematic review and avoids making definitive clinical claims.

Added in the Abstract and Conclusion:

“Among patients with NVUGIB, adjunctive medical therapy offered no clinical benefits given statistically insignificant differences in primary outcomes. However, this conclusion is limited by considerable variability in treatment protocols, weak control of confounding variables, and missing clinical information in the original studies. Notably, differences in patient characteristics (e.g., shock status, anticoagulant use, H. pylori infection) and lack of uniform dosing and timing protocols further restrict our ability to draw definitive conclusions. Therefore, while current evidence does not support the routine use of adjunctive therapy, we refrain from making broad generalizations that PPI monotherapy is universally sufficient for all NVUGIB cases. Instead, we emphasize that better-quality, large-scale randomized controlled trials are needed, ideally using standardized somatostatin dosing, timing, delivery routes, and clearly defined inclusion criteria to more accurately evaluate the role of somatostatin in NVUGIB management.”

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

No further comments are needed. The authors have fully addressed all the comments.

Reviewer 3 Report

Comments and Suggestions for Authors

The authors have made all the revisions requested. They have rewritten the discussion and conclusion to incorporate everything I pointed, especially those related to statistical, confounding bias, drug administration and evidence certainty. Thanks.