Beware of Big Gifts in Small StudiesFrom the GI-Hepatology-Nutrition Section, Washington, DC, Department of Veterans Affairs Medical Center, Washington, DC; and Georgetown University School of Medicine, Washington, DC Correspondence: Timothy O. Lipman, MD, Chief, GI-Hepatology-Nutrition Section, Department of Veterans Affairs Medical Center, 50 Irving St NW, Washington, DC 20422. Electronic mail may be sent to timothy.lipman{at}med.va.gov. In the current issue of JPEN, Tiengou and colleagues1 present a small randomized study comparing a standard isotonic tube-feeding formula vs a predigested formula for jejunal feeding of acute pancreatitis. Accepting a current mantra that many patients with acute pancreatitis should be fed jejunally, the authors sought to answer the question, what type of formula should be infused into the jejunal tube, a predigested (semi-elemental) formula or an intact formula requiring digestion (polymeric)? Reporting on 30 patients who successfully completed the study, the authors suggest that, while both formulas were well and equally tolerated, the predigested formula ensured a more favorable clinical course, as evidenced by a shorter length of hospital stay and less weight loss. How robust are these conclusions, and should we now feed every pancreatitic patient a jejunal predigested formula? I would like to approach these questions with a 3-pronged focus. How does consideration of study methodology contribute to our understanding of the strength of the conclusions? What are some questions that arise from the study? Finally, is the question asked even appropriate; where are we with respect to certainty that jejunal feeding is appropriate for acute pancreatitis? Why does study quality matter? Is not a randomized controlled trial sufficient to draw conclusions? Quality matters because it has been demonstrated by those who ponder study quality that lower-quality studies tend to demonstrate more positive outcomes; differences between approaches are less likely to be pronounced in high-quality studies.2,3 What makes a study "high quality?" A variety of measures have been proposed. A "Jadad score" was developed to assess bias in clinical trials and is often used to assess study quality.4 This system asks 3 questions: (1) was the study described as randomized; (2) was the study described as double blinded; and (3) are all participants in the trial included in the final analysis? Additional points are awarded in questions 1 and 2 with respect to appropriateness of randomization and blinding. High-quality studies have a maximum score of 5, and low-quality studies score 1 or 2. How would the present study score? Randomization appears to have occurred and to have used appropriate methodology (stratification for illness severity, centralization by an outside source, using sealed envelopes). Score 2 points. The study was said to be single blinded, but this presumably was the patient who did not know which formula he or she received. Although the authors suggest that the "clinician who decided resumption of oral feeding and discharge was not the doctor responsible for the nutrition prescription," this would imply that the feeding formula was known to clinic staff and that unintended bias could have been introduced into the evaluation. No points given. Finally, of 36 patients entered into the protocol, full data are available on only 30. The authors give data on length of stay, including all 36 as an afterthought, but full information is not available. Give 0 points for full follow-up, resulting in a final score of 2, low quality. Over the years, I have developed my own quality checklist which I teach our gastroenterology fellows and medical residents, the list being a compilation of reading points acquired or lifted from various colleagues and the literature.5 Starting with a randomized controlled clinical trial, the first question that I ask of the study is what is the question that the study asks? In order to answer a question, a question, or more specifically, a hypothesis needs to be formulated. Even more specifically, the hypothesis needs to be measurable and defined. The hypothesis cannot be a fishing expedition: what might we find if we administer a predigested formula vs a standard diet; the hypothesis must state what single result do we expect: length of stay will be shortened by 3 days, death rate will decrease from 30%–10%, infectious complications (defined) will decrease from 20%–10%, etc. Why do I look for this? Because the study's primary statistics depend on it. Because with this estimate of an effect size, a power calculation can be performed to determine a sample size: how many subjects are needed in each group to "prove" to a reasonable extent the hypothesis. So effect size, power calculation, sample size determination—all important for good study quality. If these are present, a statistical difference is most likely meaningful. If not, the difference could have occurred by chance. What are the consequences of lacking a prestudy measurable hypothesis? In the current study by Tiengou and colleagues,1 the authors claim "significance" to the shorter hospital stay in the predigested group, with a p = .006. I count 13 parameters that were measured and presented with statistical information. A colleague with much more statistical savvy than I possess rapidly calculated that there is an approximately 8% chance of finding one p = .006 if there were 13 outcomes measured. The other aspects of quality that I look for when I read a paper have been mentioned directly or indirectly in the Jadad score: (1) is there true randomization; (2) is there concealed allocation (one can have effective randomization but still "cheat" and introduce potential bias if one knows to which group subjects have been randomized); (3) is there effective blinding; (4) is there "intention-to-treat" analysis; have all the subjects who were randomized been evaluated; "cherry picking" the successes makes a questionable intervention look better than it might be; and finally, (5) is there complete follow-up of all of the study participants? What we are left with when we examine the paper by Tiengou and colleagues1 is a study with a low Jadad quality score and one with a "significant" outcome that, with 8% probability, could have occurred by chance. As the authors rightly note, with the limitations inherent in their study, the best that can be gleaned is the establishment of a hypothesis to properly power a larger clinical trial. Some other aspects of the rationale for the approach and the actual interventions caught my attention. The authors suggest that prevention of intestinal bacterial translocation is a potential mechanism by which jejunal feeding or predigested jejunal feeding promotes positive clinical outcomes in acute pancreatitis. I am continually amazed that bacterial translocation is frequently and almost ritually touted as the explanation for all things good in gastrointestinal artificial feeding. Ten years ago, I reviewed the literature concerning bacterial translocation.6 At that time, I concluded that bacterial translocation was well established in a rat model, might be species specific, was affected inconsistently by types of intestinal artificial feeding in the rat, probably existed in humans, but that there was no evidence in humans that IV artificial feeding promoted bacterial translocation or that gastrointestinal artificial feeding prevented bacterial translocation. Ten years later, I have found no evidence to alter my conclusions. Isn't it time to give bacterial translocation a merciful rest? Another aspect of critical reading skills that I try to teach our trainees is to evaluate whether the question or methods addressed in the study comport with other experience. In what now appears to be the "standard" reference, Marik and Zaloga7 performed a systematic review and meta-analysis of the literature comparing jejunal intestinal artificial feeding with IV artificial feeding in acute pancreatitis. In this article, the authors conclude (wrongfully, I think, but more on this below), that "early initiation of enteral nutrition should be considered as standard in patients with severe pancreatitis." Marik and Zaloga7 do not define "early" but suggest initiation within a "few days." Does the protocol reported in the present issue of JPEN follow this suggestion? Tucked away in the methods section is a statement that "some patients received peripheral parenteral nutrition." In fact, half of the study population received peripheral IV artificial feeding for a more than a week. Additionally, for all patients, the total number of days before insertion of the tube for nasojejunal feeding was over a week. This study, then, is no longer an evaluation of 2 feeding products after early initiation of intestinal artificial feeding in acute pancreatitis but rather it is the study of 2 products after feeding delay in patients with acute pancreatitis, many of whom who had already received a week of IV artificial feeding. How does one relate any information gleaned from this particular study to the general recommended approach of early intestinal artificial feeding? A recently published study calls into question whether jejunal feeding is even necessary, if one thinks that gastrointestinal feeding provides clinical benefit for patients with acute pancreatitis. Eatock et al8 (appropriately referenced in the current paper) found no difference in tolerance, clinical outcomes, or laboratory outcomes in 50 patients with acute pancreatitis randomly treated to either early nasogastric or nasojejunal predigested (semi-elemental) formula. The study authors concluded that early nasogastric feeding was as good as nasojejunal feeding while being useful and practical. The conclusions must be tempered by the fact that the study was underpowered to detect any clinical difference or to prove equivalence and the extremely high mortality rate (25% overall) observed in both groups. Finally, I would suggest that the route of gastrointestinal feeding and type of jejunal formula to be infused are not the questions that the artificial feeding community should be asking currently. There is no question that in selected patients early jejunal artificial feeding results in better outcomes compared with IV artificial feeding.7,9 These comparisons only tell us that one artificial feeding modality results in different outcomes than the other. Rather than intestinal being "better," IV could well be "worse." Because there is no "unfed" control group, we cannot state that artificial feeding by the intestinal route results in better, the same, or worse clinical outcomes compared with no artificial feeding. To say that the literature evaluating artificial feeding per se with respect to acute pancreatitis is sparse would be generous. To my knowledge, only 2 randomized trials compare IV artificial feeding with no artificial feeding in acute pancreatitis. Sax et al found10 that patients with acute pancreatitis who received artificial feeding had a longer duration of hospitalization and possibly more infections compared with non–artificially fed controls. Xian-li et al11 reported beneficial results from IV artificial feeding that are so far out of keeping with other reported clinical experience that it engenders disbelief. To my knowledge, there is only 1 trial addressing intestinal artificial feeding in acute pancreatitis compared with no such intervention.12 In a short-term, primarily physiologic study, intestinal artificial feeding neither ameliorated nor exacerbated the inflammatory response to acute pancreatitis, nor did it alter multiple organ-dysfunction scores. Those receiving the intervention had more abnormal intestinal permeability and more frequent nausea. It is possible that gastrointestinal artificial feeding improves clinical outcome in acute pancreatitis, but it is equally possible that intervention before 10–14 days of illness provides no benefit, or, if the 25% mortality documented by Eatock et al8 is "true," gastrointestinal artificial feeding may be harmful, just less harmful than IV artificial feeding. Certainly, evidence from controlled clinical trials in other disease states suggests that the time frame for initiating artificial feeding should be measured in terms of weeks, not days.13 Taken alone, the study by Tiengou et al1 in this month's JPEN serves to remind us of the limitations of small clinical trials. The study was underpowered to support robustly the clinical finding of a better outcome using a predigested formula infused into the jejunum and was not designed to mirror current recommendations for early intestinal feeding. At best, the findings should be taken as hypothesis generating: the potential question for the next properly powered clinical trial. However, as I have suggested, the big question is not what kind of formula should be placed into the gastrointestinal tract or where a formula should be placed in relation to the pylorus, but if any formula should be infused at all. Received for publication September 28, 2005. Accepted for publication October 11, 2005.
Journal of Parenteral and Enteral Nutrition, Vol. 30, No. 1,
66-68 (2006)
|
|
|||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||||
 |
|
|
 |
|
