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Kansagara D, Wolf F, Freeman M, et al. Management of Inpatient Hyperglycemia: A Systematic Review [Internet]. Washington (DC): Department of Veterans Affairs (US); 2008 Oct.

APPENDIX DREVIEWER COMMENTS AND RESPONSES

ReviewerCommentResponse
GENERAL COMMENTS
Question 1. Is the report well structured and organized?
Aron(Strongly agree, no comment)Noted
Pogach(Strongly agree) Follows agreed upon formatNoted
AhmannagreeNoted
Question 2. Are the main points clearly presented?
Aron(Strongly agree, no comment)Noted
Pogach(Strongly agree) Review of methodological shortcomings of available studies, and paucity of data appropriateNoted
AhmannagreeNoted
Question 3. Is the report relevant to clinical practice?
Aron(Strongly agree, no comment)Noted
Pogach(Strongly agree) Yes. This report is quite relevant to clinical practice. Hope that it gets published.Noted
AhmanndisagreeNoted
Question 4. Did the summary reflect the main points of the report?
Aron(Strongly agree, no comment)Noted
Pogach(Strongly agree, no comment)Noted
Ahmann(Agree)Noted
SCOPE AND TOPIC DEVELOPMENT
Question 1. Are the target patient populations explicitly defined?
Aron(Strongly agree, no comment)Noted
Pogach(Strongly agree, no comment)Noted
Ahmann(Agree)Noted
Question 2. Is the scope of the report clearly defined?
Aron(Strongly agree, no comment)Noted
Pogach(Strongly agree, no comment)Noted
Ahmann(Agree)Noted
Question 3. Are the key questions important and relevant?
Aron(Strongly agree, no comment)Noted
Pogach(Strongly agree, no comment)Noted
Ahmann(Disagree)Noted
Question 4. Are important clinical interventions or outcomes missing?
AronnoNoted
Pogach(No response)Noted
AhmannThis is a very difficult topic area to review and make conclusions that are relevant. I think there was inadequate attention given to the type of protocol used, the abillity to reachgoal, and the adherence to the protocol. This last point is seldom mentioned but is clearly a problem.Tables 1, 2, and 3 detail both the glucose targets as well as glucose levels achieved. We've added footnotes to Table 4 that detail the type of protocol used, and the data used to titrate insulin in each protocol. Table 5 and key questions 2 and 3 have been expanded and explore insulin infusion protocol studies in greater detail. In key question 3 and the discussion, we underscore the variability across protocols. In discussing the discrepancy in results between the Van den Berghe SICU trials and subsequent trials we acknowledge that protocol/staffing/institutional characteristics may be responsible. We disagree that this variability makes it difficult to make relevant conclusions. We discuss the view that this discrepancy in results may highlight feasibility issues with protocol implementation and may hamper broad generalizability of single-center trial results.
Question 5. Is the analytic framework useful in explaining the logic and organization of the evidence report?
Aron(Strongly agree, no comment)Noted
Pogach(Agree, no comment)Noted
Ahmann(Agree)Noted
METHODS
Question 1. Are the methods clearly stated?
Aron(Strongly agree, no comment)Noted
Pogach(Strongly agree, no comment)Noted
Ahmann(Agree) However, it isn't clear why unpublished studies (without peer review) were included unless they supported the contention of the authors.We only included unpublished studies if the authors provided either a full manuscript or enough information to quality rate the study. In essence, our critical analysis of these studies provides a peer review. This approach is accepted by peer reviewed journals - in fact, a meta-analysis on inpatient glycemic control in critically ill patients just published in JAMA included many of the same unpublished studies.
Question 2. Are the methods for identifying relevant articles adequate?
Aron(Strongly agree, no comment)Noted
Pogach(Strongly agree, no comment)Noted
Ahmann(disagree) I believe there are other articles that are relevant to hypoglycemia where the outcomes are not the primary measure for the study. In other words, the frequency of hypoglycemia is likely related to diagnosis but is also related to the virtues of the protocol used. Many of the European research studies cited used the Van den Berghe protocol for delivering insulin. This is very likely an inferior protocol and requires a lot of nursing experience to use properly. Yet, the frequency of hypoglycemia in Braithwaites work or that of the Yale group, where the goal of the effort was to find a more effective insulin infusion protocol, was not reported and would be very pertinent. The same is true for computerized algorithms which were not addressed in the second and third questions.We've expanded our discussion of these issues. See Table 5 and discussion in key questions 2 and 3.
Question 3. Are the methods for exclusion of studies appropriate?
Aron(Disagree) I think that exclusion criteria that result in the exclusion of the Furnery paper (ref. 84) are too narrow. I do appreciate that the paper was discussed, though.We have added a section presenting the results and discussing strengths/weaknesses of several frequently cited observational trials including the Furnary paper.
Pogach(Agree) The Furnary article is not randomized, but does trend improved outcomes with improved glycemic control over time, including subsequent to the implementation of the infusion. The question for me is whether or not this study sufficiently controls for other contributing factors to infections and mortality to permit a conclusion that glycemic control is an independent factor. I would prefer to see the study included and critiqued in greater detail, although I understand the rationale for exclusion.See above
We expanded our discussion of Furnary. The issue that most weakens the strength of conclusions from these studies derives from the use of historic controls. Observational studies, especially those that do not use prospective control groups, may overestimate treatment benefit. Though Furnary et al do attempt to control for severity of illness, it is possible that additional confounding factors were not accounted for. Moreover, it is very possible that regression to the mean and the effects of secular improvements in surgical and ICU care may account for a substantial proportion of the outcome improvement observed in the study.
AhmannagreeNoted
Question 4. Are the methods for grading the quality of individual studies appropriate?
Aron(Agree, no comment)Noted
Humphreymy biggest suggestion is that somehow you need to be more transparent about your quality ratings. if you have a quality table that you can include or if you can add a few qualtiy columns to your evidence tables that might be helpful. you can also just add a quality column and then use foot notes to indicate where it fell down in quality. i like a real qualtiy table much better tho.We will include our quality table as an appendix and we will describe major reasons for downgrading of quality scores in the Results section.
PogachNo responseNoted
Ahmann(disagree) Studies that are not completed due to their inability to enroll to the levels indicated by power calculations should not be weighted highly, if even reported. For example, the DIGAMI II study was clearly stopped because they couldn’t recruit (personal communication with the PI) and when they went to the multi-center approach to get a robust study, the investigators did a very poor job of getting to goal. Yet, the DIGAMI I and II trials were judged of equivalent quality. In fact, you gave far too much weight to trials where the study was stopped early and the power to make a conclusion was lost. Yet, you included those studies in your interpretation of the questions.We do now make a note of studies that were stopped early for reasons other then benefit or harm. We believe the studies are still relevant to the questions. The inclusion of other trials that were stopped early because of benefit or harm (eg - the VISEP study) we believe is justifiable because the finding of excess harm is an important finding that, if the trials are similary internally valid, should be given equal weight. Furthermore, the use of meta- analysis for the ICU studies should help improve power to detect a difference if one existed.
RESULTS - BY KEY QUESTION
Key Question 1. Does strict glycemic control compared to less strict glycemic control improve final health outcomes in the following patients?
Question 1. Is the amount of detail presented in this screening key question appropriate?
Aron(Agree)Noted
PogachVery well documentedNoted
Ahmann(Agree)Noted
Question 2. Are the summary and evidence tables clear, and/or do they highlight the main issues?
HumphreyI believe you need a little more detail in your evidence tables.We are adding a column to in-text tables detailing concomitant nutrition/therapy. Our larger parent evidence tables are available for review upon request.
Aron(Agree)Noted
Ahmann(disagree) When you agree that the GIK protocols (where glucose control was not a target) were not of benefit, how can you include them with the other protocols in deciding benefit of IIP in CABG patients. Furthermore, the Gandhi article is a study of the impact of the couple hours intra-operatively and should not be considered as an overall study of glucose control peri-operatively. These patients were all treated very aggressively after they left the OR. Also, you included far too many studies that were small (<400 patients and frequently < 100 patients) that in this format neutralize the effect of much larger studies.

Your discussion on page 19 is very biased and concerns me about the slant on the rest of the work. How can you report the results separately without the Van den Berghe results as “most directly addressing the question of efficacy” when other studies included in that meta-analysis had flaws that were greater.
We included GIK studies if they used a glucose target. We attempted to clarify this - in the last paragraph of the perioperative section, we list all the references we excluded because the intervention did not use a glucose target.
We agree that the Gandhi study examines a different time-frame for glucose control, but we do clearly note this in the text and table and we do not believe the inclusion of this study diminishes the conclusion that the body of literature examining perioperative glucose control is heterogenous, methodologically limited, and does not provide clear evidence of benefit from tight glycemic control in perioperative settings.
In terms of the size of the studies - there were no larger studies that met inclusion criteria for the perioperative subsection and this again supports the conclusion that there is limited evidence in perioperative settings.
Re: the discussion of meta-analysis results excluded Van den Berghe - we attempted to clarify the language used in the text. Essentially, excluding Van den Berghe from the meta-analysis
Question 3. What evidence have we included that ought to be excluded or down-weighted?
PogachNone.Noted
AhmannThe VISEP study was one of the few studies you rated as “good quality” but it ended far short of its power calculation (<<50%) and was actually performed using the Van den berghe protocol. I don’t understand why this study was considered better evidence than Van den Berghe’s studies. You can make conclusions about hypoglycemia for this and the GLUCONTROL but you must consider the quality of their IIP and its implementation. You cannot comment on results when these studies were not powered to find such differences in the number of patients they had at completion.We agree about the quality rating issues and we've re-evaluated all studies. We agree that the power issues for studies stopped early need to be discussed, but we disagree that results from these studies cannot be included. To help address some of these concerns we;ve added a meta-analysis of ICU studies. We discuss the power issue in the methods section as a rationale for performing meta-analysis of the ICU studies and in the discussion section as well. In terms of stopping rules and consequent power issues: the Van den Berghe SICU trial was actually also stopped short of its original recruitment goals and there is some literature suggesting that studies stopped early for benefit may overestimate treatment effects - we've added this to our discussion as well.
Question 4. Do you know of studies we have overlooked?
AronnoNoted
PogachNo.Noted
Key Question 2. What are the harms of strict glycemic control in the above subpopulations?
Question 1. Is the amount of detail presented in this treatment key question appropriate?
Aron(Agree)Noted
Pogach(Strongly agree)Noted
Ahmann(Agree)Noted
Question 2. Are the summary and evidence tables clear, and/or do they highlight the main issues?
Aron(Agree)Noted
Pogach(Strongly agree)Noted
Ahmann(disagree) More attention to the type of infusion protocol should be included to identify infusion protocols with greater risk. Also, why are some studies included on the tables referring to “frequency of hypoglycemia” when they don’t include rates of hypoglycemia? In the hypoglycemia table on “observational studies” the Krinsley experience is listed twice when one patient population is probably a subset of the other. Why are not the Goldberg articles (Yale) and North Carolina (Braithwaite) and several studies from Atlanta not included in the observational group? They are good protocols (probably far superior to the Van den Berghe protocol used in GLUCONTROL, VISEP and others).Please see comments above under scope and topic development. Originally we had intended to use existing systematic reviews as the basis for key question 3. Given the appropriate concern that more emphasis should be placed on the protocols themselves, we've added a number of studies to Table 5 (including the Goldberg and Braithwaite studies).
Question 3. What evidence have we included that ought to be excluded or down-weighted?
PogachNone.Noted
Question 4. Do you know of studies we have overlooked?
AronnoNoted
PogachnoNoted
Key Question 3. What are the most effective and safest means of lowering blood glucose in the above subpopulations?
Question 1. Is the amount of detail presented in this key question appropriate?
Aron(Disagree) details about similarities and differences among the protocols would be useful.We will add more detail to the Key Question 3 section when describing the two systematic reviews upon which this discussion is based.
Pogach(Strongly agree)Noted
Ahmann(agree)Noted
Question 2. What evidence have we included that ought to be excluded or down-weighted?
PogachNoneNoted
HumphreyYou probably need to be more clear how you came up with only 5 observational studies in the harms section. those studies look highly suspicious to me for selection bias. their rates of hypoglycemia are not believeable. i recommend leaving out the observational studies since you ahve a lot of trial data. regarding the hypoglycemia, you may want to add more to the text about the degree of hypoglycemia most studies counted. it seems fairly extreme. my guess is that there was a lot of hypoglycemia in the 60 80 range.We had excluded several observational studies because they reported hypoglycemia rates per number of glucose measurements rather than per person. We will clarify this in the text, reference these additional studies and also present their rates of hypoglycemia (while making it clear that reported rates use different denominators). We do think that it is appropriate to include observational trials for the harms question as these trials add information about "real-life" utility of these protocols. In terms of the definition of hypoglycemia in each study, this information is presented in a column within the in-text hypoglycemia table.
AhmannNo discussion of computerized models or the different types of protocols that have been used.Two studies met inclusion and are added to Table 5 and we also mention this as an area for future research.
Question 3. Do you know of studies we have overlooked?
PogachNoneNoted
CONCLUSIONS AND FUTURE RESEARCH
Question 1. Are the implications of the major findings clearly stated?
Aronstrongly agreeNoted
Pogachstrongly agreeNoted
Ahmann(disagree) I think there should be more emphasis on the real questions that are raised by the studies that have been done. One would come out concluding that the evidence says intensive insulin therapy in the hospital is not supported by the literature but the literature is inadequate.
I think the real questions are
 What should the target be?
 What types of approaches help us to get there safely and effectively?
Importantly, the recent studies that failed to show a benefit of intensive control compared the “intensive group” to a level of control that is actually quite good. The glucose level sought in the control group is much better than the standard of the past. Furthermore, these were not completed studies. Maybe the goal should be 100–150 but that is not determined by any of the studies.
Also, how long does it take to get to goal? How much glucose variability is there when you get to goal? How much of this is due to nursing error because of poor inservice education or complexity of the protocol?
These and many other questions are important? Obviously it is not black and white when you consider all of the permutations of the studies that have been done.
We agree that the literature to date does not answer what the glucose target should be. We suggest that the literature to date does not support widespread application of a normal glucose target in ICU patients as has been supported in some guideline recommendations. We tried to clarify in our discussion and conclusion that the literature simply does not tell us much about higher targets. The conclusion reads as follows: The use of intensive insulin therapy to achieve normoglycemia in critically ill patients does not clearly result in health outcome benefits and is associated with high rates of hypoglycemia. More moderate blood glucose control to targets above the normoglycemic range can likely be safely achieved, though the health outcome benefit of this practice has not been well studied.
Re: variability issues - discussed in several comments above. We added some language to key question 3 and the discussion suggesting that this variabilitiy underscores the complexity of instituting insulin infusion protocols.
Question 2. Has the evidence report dealt adequately with the gaps in the literature?
AronagreeNoted
Pogachstrongly agreeNoted
AhmannagreeNoted
Question 3. Does the evidence report highlight all the appropriate main conclusions and considerations for future research?
AronagreeNoted
Pogachstrongly agreeNoted
Question 4. Does the summary and benefits of harms section adequately address the issues?
Pogachstrongly agreeNoted
ADDITIONAL COMMENTS
PogachPage iv, line 16 section and related sections. The framing of the results is important. I would concur with the issues regarding the efficacy of “tight” control. However, the question is whether or not there is sufficient evidence to make a statement regarding improved control? As opposed to not treating hyperglycemia.The summary paragraph at the beginning of the Key Question 1 exec summary section (page iv, lines 10–12) does say that the impact of lowering glucose to higher targets is uncertain. We will also clarify in the following paragraph that most ICU studies targeted normoglycemia.
Humphrey3. in general i think you would do well by adding a few subtitles to keep readers very clear about what you are talking about as it is easy to get lost in the detail.,
4. i like figure 2 alot,
6. be sure to add the stroke data to table 3, ref 15.(evidence table 2?).
7. you probably could add a few more outcomes to the table also if you wanted. you discuss more of them in the text than are in the table. maybe under another column.
3 - we will add more subheadings
4 - thank you
6 - will add
7 - some additional outcomes are mentioned under a comments heading. The parent evidence table includes all of this information. The presented tables are meant to be in-text tables, so space will be limited.
RenderExecutive Summary, MICU/SICU: Concerns with the Brunkhorst study. 1) underpowered 2) unclear if there was a significant difference in glycemic control between the 2 groups since they only provide information about AM glucose. What about glucose values the rest of the day? Regarding the Van den Berghe studies, the bulk of mortality reduction in the SICU study came from those long-stay patients and the absolute reduction in mortality for MICU and SICU long stay patients is basically equal.The individual studies are discussed in more detail in the full report (there simply wasn't space in the executive summary to provide all relevant information). For Brunkhorst, we clarify the number of patients included vs number projected in the results section.
The reporting of mean AM blood glucose was common to most of the ICU studies, including the two Van der Berghe studies. The relative decrease in AM blood glucose in Brunkhorst was comparable to the Van der Berghe SICU study.
The issue of the long-stay subgroup benefit is discussed in our full report.
Render
The trials that did indeed focus on glycemic control using adjustable dose insulin are limited by methodologic problems. One example is DIGAMI 2 which was not able, again, to establish real glycemic differences between groups, was underpowered, and randomized < 50% of patients.
We agree that there are methodologic issues that limit the strength of the conclusions and we do acknowledge this in the exec summary ("…but variation in trial design, achievement of recruitment goals, glucose level achieved, and concomitant therapy for MI limit the strength of this conclusion."). These limitations are further detailed in the full report.
RenderExecutive Summary, CABG: The Gandhi study was looking at intraoperative control. ALL patients received glycemic control post-operatively. So the intervention lasted a few hours. The study was not powered to show a difference in mortality and it would be expected that a few hours of glycemic control beyond the tight control that all patients already receive post-op would not make a difference.We agree that the Gandhi study (and others) were likely underpowered to show differences in final health outcomes and this is acknowledged in the exec summary and full report. The study details are presented in the full report. We will clarify in the report that this study was really designed to look at the effect of intraoperative control on patient outcomes. We do believe the outcomes as reported are still important to present while acknowledging the contextual methodologic considerations.
RenderKey Question 3: I have attached a reference list (some studies, some just opinion or review) addressing sliding scale. The Queale and Umpierrez studies suggest sliding scale monotherapy is not safe or effective.Thank you for the reference list. We relied on two recent systematic reviews for our key question 3 discussion. We agree that limited evidence suggests basal-bolus regimens may be more effective than sliding scale. We do present more detail in the body of the report and will add additional references if there are controlled clinical trials examining sliding scale insulin that we missed.
RenderThe overall limitation of this position statement/summary is that in answering question #1, it ignores data from well conducted observational studies suggesting that hyperglycemia is harmful (especially for AMI). The problem with relying on RCTs that attempt to address whether glycemic control in the ICU is beneficial is that most trials, even multi-center studies, have been ineffective due to difficulty achieving adequate power and/or establishing glycemic differences between study groups.In our introduction, we do report there is a body of evidence suggesting an association between hyperglycemia and poor outcomes in various inpatient subpopulations. We disagree that this body of evidence (eg - the Capes systematic reviews) can be extrapolated to answer the question of whether or not intervening with intensive insulin therapy will result in improved outcomes. In terms of evaluating other observational trials that examine the effects of intensive insulin therapy, there are several that are frequently cited and will be discussed in the revised report.
Barrett1. Some of the questions, e.g. Key Q 1 subpopulation any ward patient, and Key Q 3 did not require a systematic review to answer as there is almost no data. Consideration in highlighting this including not having them as questions may be given. I would be concerned about mis-interpretation of results and importance with repeated mentioning of these categories throughout the document giving them as much weight it would seem at times as the other Key Qs that did have data.We agree there are limited data in these subpopulations. The key questions were developed based on input from those commissioning the report. In situations in which there are limited data, we believe that clearly defining the limitations of the literature after a systematic search may help direct future research efforts and clinical applicability of currently available data.
Barrett2. The different inclusion criteria for Key Q 2 (Harm) makes the document biased by definition. Data is just data, why not treat all the questions the same? The issue of harm in particular is controversial, so I understand why you would want to include more obs data, but then why not include the same quality obs data for the rest of the Qs?There are numerous precedents for using observational data to investigate harms in systematic reviews and our current methods manual supports this approach when efficacy studies don't adequately address harms. In this case, we felt investigating hypoglycemia rates in observational studies (and trials without health outcomes) would also contribute valuable information about the feasibility of IIT in various settings since hypoglycemia is
Barrett3. The reference to Furary I believe is this: Zerr KJ, Furnary AP, Grunkemeier GL, Bookin S, Kanhere V, Starr A. Glucose control lowers the risk of wound infection in diabetics after open heart operations. Ann Thorac Surg. 1997 Feb;63(2):356–6. Your reference was from 2006. As we discussed, this paper in 1997 (over 10 years ago) started the entire inpatient tight glycemic control movement. The systematic review should dwell more on this paper and perhaps state that if you were to include the data from this paper it would/would not change your recommendation. It is a cultural thing and will be a major critique of the systematic review unless you address it fully.See above - we expanded our discussion of Furnary and other observational studies. The references chosen contributed the most up-to-date data from the studies.
AhmannI realize this is a very difficult process and the studies are really not comparable. They have different populations, use different tools that vary in complexity and effectiveness, report different outcomes (including variable ways of reporting glucose and hypoglycemia rates), and probably represent highly variable nursing performance for utilizing the protocols properly.

I personally don’t think the goal is 110 mg/dl but we have to be careful not to leave the impression that inattention to glucose control is the goal supported by the evidence. Highlighting the limitations of studies and trying to find those few things that we can conclude should be the most clear messages. For example, GIK infusions are not useful. The studies don’t help us determine the optimal goals. Period!
The report was commissioned to determine the state of the evidence and is not intended to serve as a clinical guideline. We agree that ultimately, implementation decisions will need to take into account the variability in practice (eg - acknowledge local nursing performance/resources etc).

Reviewers

AhmannAndrew Ahmann, MD
AronDavid Aron, MD
BarrettTom Barrett, MD
HumphreyLinda Humphrey, MD, MPH
PogachLeonard Pogach, MD
RenderMarta Render, MD
Cover of Management of Inpatient Hyperglycemia
Management of Inpatient Hyperglycemia: A Systematic Review [Internet].
Kansagara D, Wolf F, Freeman M, et al.
Washington (DC): Department of Veterans Affairs (US); 2008 Oct.

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