552849
research-article2015
PENXXX10.1177/0148607114552849Journal of Parenteral and Enteral NutritionKoretz
Journal Club Journal of Parenteral and Enteral Nutrition Volume 39 Number 2 February 2015 228–230 © 2015 American Society for Parenteral and Enteral Nutrition DOI: 10.1177/0148607114552849 jpen.sagepub.com hosted at online.sagepub.com
JPEN Journal Club 10. Blinding Ronald L. Koretz, MD1
The article to be considered in this installment of the JPEN Journal Club evaluates the use of a dietary intervention to treat irritable bowel syndrome (IBS). As a prelude to discussing this treatment for IBS, let us reflect on the underlying pathophysiology. It would be incorrect to presume that patients with IBS have a disease that is “in their heads.” These patients have symptoms because of some altered intestinal sensory capacity. Among other things, they do seem to be overly sensitive to intestinal distension. It has been speculated that nonabsorbed short-chain carbohydrates reach the colon where they are metabolized by bacteria, resulting in the production of various gas products and a hyperosmotic liquid; both of these phenomena then produce colonic luminal expansion and consequent symptoms. The family of such carbohydrates has become known as fermentable oligosaccharides, disaccharides, monosaccharides, and polyols (FODMAPs). FODMAPs include fructose (in excess of glucose), lactose, polyols, fructans, and galacto-oligosaccharides. Halmos and her Australian colleagues tested the hypothesis that removing FODMAPs from the diet would have therapeutic benefits in relieving the symptoms of IBS.1 To address this question, they undertook a single-blinded randomized crossover trial. “Blinding” is a term that refers to preventing various parties involved in a trial from knowing which intervention is being provided. When investigators design a trial, they decide whom they want to be blinded. The parties who can be blinded are the study subjects, the investigators providing the intervention, and the people who assess the outcome. (Not uncommonly, the last 2 groups are composed of the same individuals.) Usually, a single-blinded trial conceals the knowledge of the intervention only from the study subjects, whereas a double-blinded trial also prevents the investigators/assessors from knowing what is being administered to each subject. (There might be rare situations in which single-blinding could refer to withholding the knowledge of the treatment from the investigators/assessors but not the subjects.) Crossover trials should be distinguished from parallel group trials. In the latter, subjects are assigned to receive only 1 of the possible interventions. In crossover trials, the subjects are sequentially exposed to all of the interventions that are being assessed and thus act as their own controls. To get around any effect that would influence subsequent interventional challenges (e.g., learning or adaptation), the order of
the challenges should be determined by randomization. The major advantages to crossover trials are that a lower number of patients needs to be enrolled and that the 2 groups will be quite comparable (identical, in fact), eliminating confounding factors.2 A limitation of such trials is that the investigators have to be sure that the second intervention is not influenced by some residual effect of the first intervention. The time that is allotted for any residual effect to be lost is referred to as the “washout period.” A crossover design may be suitable if the outcome occurs relatively quickly (eg, days or a few weeks); it is not an appropriate design for any intervention that has a long-lasting effect. In the FODMAP trial, 33 patients with IBS were initially enrolled, but 3 dropped out because of intolerance of, or noncompliance with, the diets. Thus, 30 subjects completed both arms of the trial. Good methodology was generally employed; the randomization sequence was generated by a computer, there was adequate concealment of allocation, an effort was made to blind the subjects, all of those subjects were accounted for, appropriate outcomes were reported, and a sample size calculation was performed. The primary outcome was the level of overall relief from gastrointestinal symptoms as measured on a 100-point scale, with a lower numerical score correlating with fewer symptoms. The average symptom score on the low FODMAP diet was 23, a number that was significantly lower than the average score of 45 when the patients were consuming
From the 1Olive View–UCLA Medical Center, David Geffen–UCLA School of Medicine, Sylmar and Los Angeles, California. Financial disclosure: Dr Koretz receives ongoing support from GIIssues, Inc, a 401(c)(3) nonprofit organization that promotes the use and dissemination of evidence-based medicine. While no particular funds were used for this particular project, GIIssues, Inc, will support Dr Koretz’s academic travel, society memberships, and other academic activities that have some relationship to the mission of the promulgation of evidence-based medicine. GIIssues, Inc, does not provide any salary support for Dr Koretz. Received for publication August 22, 2014; accepted for publication August 27, 2014. Corresponding Author: Ronald L. Koretz, MD, Olive View–UCLA Medical Center, 14445 Olive View Drive, Sylmar, CA 91342, USA. Email: [email protected]
Downloaded from pen.sagepub.com at University of British Columbia Library on June 23, 2015
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the control diet, referred to as “a typical Australian diet.” A number of secondary outcomes also improved with the low FODMAP diet, including bloating, pain, and passage of flatus. The investigators concluded that there was now high-quality evidence to support a policy of using a low FODMAP diet as first-line therapy in patients with IBS. How reliable is this recommendation? In other words, are there any limitations to this trial that would undermine the conclusions of the investigators? If the symptom score does reflect the influence of dietary FODMAPs, it should be noted that the average score of the patients at baseline, before the trial began, was 36, which is a number between 23 and 45. Thus, it may be that the Australian diet did not match what the patients had been eating on their own. Although the investigators did state that the score on the low FODMAP diet was lower than the baseline score, they did not provide any statistical analysis to demonstrate whether that difference was significant or not. In any event, it may be that this diet will be less effective in patients who have, on their own, made some modifications to their own diets. Another potential problem was that patients with known fructose intolerance were not excluded from the trial. Since part of the intervention was the removal of fructose from the diet, the benefit may not have been from eliminating all of the FODMAPs but just from eliminating fructose. An issue that frequently arises in parallel group randomized trials is that of dropouts in one or the other treatment arm. The one time when we are most assured that the randomization is intact (ie, we are reasonably assured that there are no confounding factors) is when the patients are initially assigned to the treatment arms. When patients drop out, we cannot always be sure that the dropouts did not create some type of imbalance in the arms that reintroduced confounding. In a crossover trial, a dropout in one arm is precisely matched by a dropout in the other arm, and no such problem with confounding exists. Unfortunately, dropouts in crossover trials may create other problems. The original subjects were drawn from some defined population; dropouts may change the characteristics of that population such that the effect is no longer extrapolatable.3 In the FODMAP trial, the dropouts appear to have represented the segment of the population that would be more resistant to complying with the experimental diet. Thus, the measured effect may have overestimated the true effect. The reason that I selected this article was to consider the issue of blinding. The principal reason to worry about blinding is in interpreting the outcomes. If the outcome is something that is objectively measurable, such as a lab test or a death, it is often said that blinding is not important. However, even this may not be true, as such factors as compliance to the intervention may depend on the vested interests of the subject or investigator. It is entirely possible that knowledge of what
intervention is being provided may lead to different degrees of adherence to the treatment regimen. Certainly, if the outcome is subjective, such as pain, knowledge of the intervention is of major importance with regard to introducing bias4; blinding is always needed if one is measuring subjective outcomes. In this regard, we should remember that even quantifiable data can be subjective. Consider length of stay in a hospital; the decision to discharge a patient is actually a subjective one, even if the number of days that the patient spends confined in the hospital is then precisely measured. Trials in IBS present a number of methodologic difficulties5; the routine use of subjective outcomes is one of the major ones. In the low FODMAP trial, the investigators did attempt to blind the study subjects by providing almost all of their food as frozen meals. In addition, the patients were allegedly naïve to the diet. The investigators further asserted that the blinding was successful because of the observation that there was no “order effect.” An order effect would occur if the effect of the active intervention or control during the first challenge was different from what it was in the second challenge. If, during the first challenge, the patients figured out which intervention they were receiving, they would then know, even before the second intervention was provided, what they were going to receive next. Thus, their expectations for the second challenge would be different than they were for the first, and a different effect might be seen in the recipients of both the active intervention and the control intervention. In this trial, the blinding was not successful. Certainly, the diets had overtly different contents that should have been easily recognized by the subjects. Since almost half of the subjects had had a previous breath test and had been instructed about FODMAPs at that time, it is probable that they recognized that diet when it was presented. Most importantly, we know that 25 of the 30 subjects recognized which diet was the one that was low in FODMAPs. (It could be argued that the blind was broken because the symptoms were dramatically improved, but, given the fact that the differences compared with baseline were less impressive, this would seem to be a less likely explanation.) The absence of blinding substantially limits the value of the observation of benefit and thus undermines the recommendation of the investigators. At least, this is true from a critical reading perspective. On the other hand, from a contextual perspective, we should remember that we are considering treatments for IBS. IBS is not a fatal disease. Its clinical importance relates solely to the symptoms that its sufferers experience. If an intervention is relatively inexpensive and nontoxic, we are often very happy to use it to improve symptoms regardless of whether or not that effect is a “placebo” one. Thus, critical reading aside, if the low FODMAP diet can be tolerated by the patient, there is no compelling reason not to use it.
Downloaded from pen.sagepub.com at University of British Columbia Library on June 23, 2015
230
Journal of Parenteral and Enteral Nutrition 39(2)
For the next installment, please read the following article: Van den Berghe G, Wouters P, Weekers F, et al. Intensive insulin therapy in critically ill patients. N Engl J Med. 2001;345:1359-1367. I encourage you and your colleagues to discuss this journal club installment online in A.S.P.E.N.’s journal club forum at www.community.nutritioncare.org.
References 1. Halmos EP, Power VA, Shepherd SJ, Gibson PR, Muir JG. A diet low in FODMAPs reduces symptoms of irritable bowel syndrome. Gastroenterology. 2014;146:67-75.
2. Koretz RL. JPEN Journal Club 3. When and why to randomize. JPEN J Parenter Enteral Nutr. 2014;38:400-401. 3. Schultz KF, Grimes DA. Sample size slippages in randomized trials: exclusions and the lost and wayward. Lancet. 2002;359:781-785. 4. Hrobjartsson A, Thomsen ASS, Emanuelsson F, et al. Observer bias in randomised clinical trials with binary outcomes: systematic review of trials with both blinded and non-blinded outcome assessors. BMJ. 2012;344:e1119. 5. Triantafyllou K. Problems and challenges in the design of irritable bowel syndrome clinical trials: focusing on the future with the experience from the past. Ann Gastroenterol. 2002;15:263-270.
Downloaded from pen.sagepub.com at University of British Columbia Library on June 23, 2015
research-article2015
PENXXX10.1177/0148607114552849Journal of Parenteral and Enteral NutritionKoretz
Journal Club Journal of Parenteral and Enteral Nutrition Volume 39 Number 2 February 2015 228–230 © 2015 American Society for Parenteral and Enteral Nutrition DOI: 10.1177/0148607114552849 jpen.sagepub.com hosted at online.sagepub.com
JPEN Journal Club 10. Blinding Ronald L. Koretz, MD1
The article to be considered in this installment of the JPEN Journal Club evaluates the use of a dietary intervention to treat irritable bowel syndrome (IBS). As a prelude to discussing this treatment for IBS, let us reflect on the underlying pathophysiology. It would be incorrect to presume that patients with IBS have a disease that is “in their heads.” These patients have symptoms because of some altered intestinal sensory capacity. Among other things, they do seem to be overly sensitive to intestinal distension. It has been speculated that nonabsorbed short-chain carbohydrates reach the colon where they are metabolized by bacteria, resulting in the production of various gas products and a hyperosmotic liquid; both of these phenomena then produce colonic luminal expansion and consequent symptoms. The family of such carbohydrates has become known as fermentable oligosaccharides, disaccharides, monosaccharides, and polyols (FODMAPs). FODMAPs include fructose (in excess of glucose), lactose, polyols, fructans, and galacto-oligosaccharides. Halmos and her Australian colleagues tested the hypothesis that removing FODMAPs from the diet would have therapeutic benefits in relieving the symptoms of IBS.1 To address this question, they undertook a single-blinded randomized crossover trial. “Blinding” is a term that refers to preventing various parties involved in a trial from knowing which intervention is being provided. When investigators design a trial, they decide whom they want to be blinded. The parties who can be blinded are the study subjects, the investigators providing the intervention, and the people who assess the outcome. (Not uncommonly, the last 2 groups are composed of the same individuals.) Usually, a single-blinded trial conceals the knowledge of the intervention only from the study subjects, whereas a double-blinded trial also prevents the investigators/assessors from knowing what is being administered to each subject. (There might be rare situations in which single-blinding could refer to withholding the knowledge of the treatment from the investigators/assessors but not the subjects.) Crossover trials should be distinguished from parallel group trials. In the latter, subjects are assigned to receive only 1 of the possible interventions. In crossover trials, the subjects are sequentially exposed to all of the interventions that are being assessed and thus act as their own controls. To get around any effect that would influence subsequent interventional challenges (e.g., learning or adaptation), the order of
the challenges should be determined by randomization. The major advantages to crossover trials are that a lower number of patients needs to be enrolled and that the 2 groups will be quite comparable (identical, in fact), eliminating confounding factors.2 A limitation of such trials is that the investigators have to be sure that the second intervention is not influenced by some residual effect of the first intervention. The time that is allotted for any residual effect to be lost is referred to as the “washout period.” A crossover design may be suitable if the outcome occurs relatively quickly (eg, days or a few weeks); it is not an appropriate design for any intervention that has a long-lasting effect. In the FODMAP trial, 33 patients with IBS were initially enrolled, but 3 dropped out because of intolerance of, or noncompliance with, the diets. Thus, 30 subjects completed both arms of the trial. Good methodology was generally employed; the randomization sequence was generated by a computer, there was adequate concealment of allocation, an effort was made to blind the subjects, all of those subjects were accounted for, appropriate outcomes were reported, and a sample size calculation was performed. The primary outcome was the level of overall relief from gastrointestinal symptoms as measured on a 100-point scale, with a lower numerical score correlating with fewer symptoms. The average symptom score on the low FODMAP diet was 23, a number that was significantly lower than the average score of 45 when the patients were consuming
From the 1Olive View–UCLA Medical Center, David Geffen–UCLA School of Medicine, Sylmar and Los Angeles, California. Financial disclosure: Dr Koretz receives ongoing support from GIIssues, Inc, a 401(c)(3) nonprofit organization that promotes the use and dissemination of evidence-based medicine. While no particular funds were used for this particular project, GIIssues, Inc, will support Dr Koretz’s academic travel, society memberships, and other academic activities that have some relationship to the mission of the promulgation of evidence-based medicine. GIIssues, Inc, does not provide any salary support for Dr Koretz. Received for publication August 22, 2014; accepted for publication August 27, 2014. Corresponding Author: Ronald L. Koretz, MD, Olive View–UCLA Medical Center, 14445 Olive View Drive, Sylmar, CA 91342, USA. Email: [email protected]
Downloaded from pen.sagepub.com at University of British Columbia Library on June 23, 2015
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229
the control diet, referred to as “a typical Australian diet.” A number of secondary outcomes also improved with the low FODMAP diet, including bloating, pain, and passage of flatus. The investigators concluded that there was now high-quality evidence to support a policy of using a low FODMAP diet as first-line therapy in patients with IBS. How reliable is this recommendation? In other words, are there any limitations to this trial that would undermine the conclusions of the investigators? If the symptom score does reflect the influence of dietary FODMAPs, it should be noted that the average score of the patients at baseline, before the trial began, was 36, which is a number between 23 and 45. Thus, it may be that the Australian diet did not match what the patients had been eating on their own. Although the investigators did state that the score on the low FODMAP diet was lower than the baseline score, they did not provide any statistical analysis to demonstrate whether that difference was significant or not. In any event, it may be that this diet will be less effective in patients who have, on their own, made some modifications to their own diets. Another potential problem was that patients with known fructose intolerance were not excluded from the trial. Since part of the intervention was the removal of fructose from the diet, the benefit may not have been from eliminating all of the FODMAPs but just from eliminating fructose. An issue that frequently arises in parallel group randomized trials is that of dropouts in one or the other treatment arm. The one time when we are most assured that the randomization is intact (ie, we are reasonably assured that there are no confounding factors) is when the patients are initially assigned to the treatment arms. When patients drop out, we cannot always be sure that the dropouts did not create some type of imbalance in the arms that reintroduced confounding. In a crossover trial, a dropout in one arm is precisely matched by a dropout in the other arm, and no such problem with confounding exists. Unfortunately, dropouts in crossover trials may create other problems. The original subjects were drawn from some defined population; dropouts may change the characteristics of that population such that the effect is no longer extrapolatable.3 In the FODMAP trial, the dropouts appear to have represented the segment of the population that would be more resistant to complying with the experimental diet. Thus, the measured effect may have overestimated the true effect. The reason that I selected this article was to consider the issue of blinding. The principal reason to worry about blinding is in interpreting the outcomes. If the outcome is something that is objectively measurable, such as a lab test or a death, it is often said that blinding is not important. However, even this may not be true, as such factors as compliance to the intervention may depend on the vested interests of the subject or investigator. It is entirely possible that knowledge of what
intervention is being provided may lead to different degrees of adherence to the treatment regimen. Certainly, if the outcome is subjective, such as pain, knowledge of the intervention is of major importance with regard to introducing bias4; blinding is always needed if one is measuring subjective outcomes. In this regard, we should remember that even quantifiable data can be subjective. Consider length of stay in a hospital; the decision to discharge a patient is actually a subjective one, even if the number of days that the patient spends confined in the hospital is then precisely measured. Trials in IBS present a number of methodologic difficulties5; the routine use of subjective outcomes is one of the major ones. In the low FODMAP trial, the investigators did attempt to blind the study subjects by providing almost all of their food as frozen meals. In addition, the patients were allegedly naïve to the diet. The investigators further asserted that the blinding was successful because of the observation that there was no “order effect.” An order effect would occur if the effect of the active intervention or control during the first challenge was different from what it was in the second challenge. If, during the first challenge, the patients figured out which intervention they were receiving, they would then know, even before the second intervention was provided, what they were going to receive next. Thus, their expectations for the second challenge would be different than they were for the first, and a different effect might be seen in the recipients of both the active intervention and the control intervention. In this trial, the blinding was not successful. Certainly, the diets had overtly different contents that should have been easily recognized by the subjects. Since almost half of the subjects had had a previous breath test and had been instructed about FODMAPs at that time, it is probable that they recognized that diet when it was presented. Most importantly, we know that 25 of the 30 subjects recognized which diet was the one that was low in FODMAPs. (It could be argued that the blind was broken because the symptoms were dramatically improved, but, given the fact that the differences compared with baseline were less impressive, this would seem to be a less likely explanation.) The absence of blinding substantially limits the value of the observation of benefit and thus undermines the recommendation of the investigators. At least, this is true from a critical reading perspective. On the other hand, from a contextual perspective, we should remember that we are considering treatments for IBS. IBS is not a fatal disease. Its clinical importance relates solely to the symptoms that its sufferers experience. If an intervention is relatively inexpensive and nontoxic, we are often very happy to use it to improve symptoms regardless of whether or not that effect is a “placebo” one. Thus, critical reading aside, if the low FODMAP diet can be tolerated by the patient, there is no compelling reason not to use it.
Downloaded from pen.sagepub.com at University of British Columbia Library on June 23, 2015
230
Journal of Parenteral and Enteral Nutrition 39(2)
For the next installment, please read the following article: Van den Berghe G, Wouters P, Weekers F, et al. Intensive insulin therapy in critically ill patients. N Engl J Med. 2001;345:1359-1367. I encourage you and your colleagues to discuss this journal club installment online in A.S.P.E.N.’s journal club forum at www.community.nutritioncare.org.
References 1. Halmos EP, Power VA, Shepherd SJ, Gibson PR, Muir JG. A diet low in FODMAPs reduces symptoms of irritable bowel syndrome. Gastroenterology. 2014;146:67-75.
2. Koretz RL. JPEN Journal Club 3. When and why to randomize. JPEN J Parenter Enteral Nutr. 2014;38:400-401. 3. Schultz KF, Grimes DA. Sample size slippages in randomized trials: exclusions and the lost and wayward. Lancet. 2002;359:781-785. 4. Hrobjartsson A, Thomsen ASS, Emanuelsson F, et al. Observer bias in randomised clinical trials with binary outcomes: systematic review of trials with both blinded and non-blinded outcome assessors. BMJ. 2012;344:e1119. 5. Triantafyllou K. Problems and challenges in the design of irritable bowel syndrome clinical trials: focusing on the future with the experience from the past. Ann Gastroenterol. 2002;15:263-270.
Downloaded from pen.sagepub.com at University of British Columbia Library on June 23, 2015
