The term “evidence-based medicine” was first coined by Sackett et al1 as “the conscientious, explicit and judicious use of current best evidence in making decisions about the care of individual patients.” The key to practicing evidence-based medicine is applying the best current knowledge to decisions in individual patients. For clinicians to practice evidence-based medicine, they must have the skills to read and interpret the medical literature so that they can determine the validity, reliability, credibility, and utility of individual articles.
Evidence-Based Reviews in Surgery (EBRS) is a web-based platform (http://ebrs.online) supported by an educational grant from Medtronic and the Canadian Association of General Surgeons. The primary objective of this initiative is to help practicing surgeons and general surgery residents improve their critical appraisal skills. During an academic year, important studies in the surgical literature are chosen for review and discussions of merits/flaws, which are encouraged on the forum. Methodological and clinical reviews of the article are performed by experts in the relevant areas and posted on the EBRS website. Surgeons who participate in the current modules can receive CME credits.
For further information about EBRS, please contact us at email@example.com
1. Evidence Based Medicine Working Group. Evidence-based medicine. JAMA 1992;268:2420-25
Despite multiple meta-analyses1–3 and retrospective population-based studies4–6 reporting the benefits of early cholecystectomy for acute cholecystitis, surgeons have been slow to change practice. A recent observational study of acute cholecystitis patients demonstrated that only 53% in the United States and 16% in England underwent emergency cholecystectomy.7 Although times have changed since the introduction of laparoscopic cholecystectomy in the late eighties, the dogma of delaying treatment has endured. Whereas early adopters of the procedure experienced barriers relating to lack of basic training in laparoscopy, general surgical residents today are facile with minimally invasive surgical procedures. In fact, laparoscopic cholecystectomy is the most common minimally invasive operation performed among general surgery residents, comprising nearly 50% of their minimally invasive cases.8 Nonetheless, surgeons have yet to widely implement early cholecystectomy and additional randomized trials continue to be performed.
Roulin et al9 have added their single-center, parallel-group randomized controlled trial (RCT) to the mounting evidence for early laparoscopic cholecystectomy (ELC) over delayed laparoscopic cholecystectomy (DLC) in adult patients with acute cholecystitis. However, their trial differs from preceding trials in that they focused on an important but previously unstudied subgroup of patients. They evaluated patients with symptoms of acute cholecystitis beyond 72 hours before hospital presentation. The trial required that patients meet Tokyo guidelines for the diagnosis of acute cholecystitis; patients were required to have local (ie, Murphy sign) and systemic (ie, fever, elevated C-reactive protein, or leukocytosis) signs of inflammation and sonographic confirmation of acute cholecystitis.10 Patients were excluded for severe sepsis, immunosuppression, perforated cholecystitis, biliary peritonitis, cholangitis, acute pancreatitis, and pregnancy. Of note, the most recent Tokyo guidelines still support delayed cholecystectomy.10
WHAT ARE THE SOURCES AND DIRECTION OF BIAS?
Overall, the trial was of high methodological quality and adhered to the Consolidated Standards of Reporting Trials (CONSORT) guidelines.11 The authors used shuffled sealed opaque envelopes containing treatment assignments to ensure adequate randomization and allocation concealment. Randomization serves to reduce selection bias by minimizing imbalances in known and unknown confounders between treatment groups. Using a valid method for randomizing patients ensures allocation concealment, or that treatment assignment cannot be predicted. Although sealed envelopes is an acceptable methodology,12 additional safeguards that could have been employed to ensure allocation concealment include (1) sequentially numbering the envelopes13 and (2) having the study nurse complete an audit sheet before opening the envelope deciding treatment allocation.14
The adequacy of randomization can be judged by determining the similarity in baseline characteristics between patients in each treatment arm at the start of the trial. In general, baseline characteristics between the ELC and DLC groups were similar. There were a slightly higher proportion of patients receiving ELC who had hypertension (36% vs 27%), pulmonary disease (12% vs 5%), and history of cerebrovascular attack (5% vs 0). However, the majority of patients in both groups had an American Society of Anesthesiologists (ASA) grade of I-II (95% in both groups). Of note, although P values are reported by the authors in comparing baseline characteristics, these should be interpreted with caution. P values represent the likelihood that an observed difference or greater occurred by chance alone assuming a null hypothesis that there is no difference between the groups. However, in a randomized trial, any differences in baseline characteristics should be due to chance alone. Therefore, the P values are not meaningful. Rather, the answer to the question of whether the groups are similar at the start of the trial should be based on whether there is a clinically important difference in that characteristic between groups and the prognostic importance of that characteristic. As noted in the CONSORT Explanation and Elaboration document, “Tests of baseline differences are not necessarily wrong, just illogical. Such hypothesis testing is superfluous and can mislead investigators and their readers.”15
Patients, clinicians, and study personnel were not blinded to treatment. Given the difference in timing of the interventions, it would not have been possible to blind the patients or the providers as to treatment assignment. It would also have been difficult to blind outcome assessors given that the primary outcome included unplanned readmissions and emergency consultations before cholecystectomy. Data analysts could have been blinded.
All patients who were randomized were accounted for on follow-up. Furthermore, an intention-to-treat (ITT) analysis was performed, which means that all patients were analyzed in the group to which they were randomized regardless of whether or not they received the treatment. One patient allocated to ELC and 6 patients allocated to DLC did not receive the assigned treatment. An ITT analysis allows for maintenance of balance in baseline characteristics achieved by randomization, and it is the primary analysis for superiority trials.
WHAT WERE THE RESULTS AND WERE ALL CLINICALLY IMPORTANT OUTCOMES CONSIDERED?
The primary outcome was a composite of overall morbidity defined as treatment failures, unplanned readmissions, and emergency consultations before cholecystectomy, and 30-day postoperative complications. This primary outcome was specifically chosen to represent the patients’ point of view or as a patient-centered outcome. This is especially important in an era when clinical care is increasingly focused on patients themselves, as opposed to traditional drivers such as surgeon preference or resource allocation. The frequency of “non-resolution” of symptoms during the waiting period for a delayed cholecystectomy was 30%, which is higher than a prior estimate of 18% from a Cochrane review.2 From a patient perspective, this represents poor quality of care in terms of timeliness and efficiency. Furthermore, although patient-reported outcomes such as return to work and normal daily activities were not collected in this trial, the longer time to cholecystectomy and longer hospital stay most likely impeded patients’ return to usual health.
Overall, ELC resulted in a large treatment effect: a 74% relative reduction and a 24% absolute reduction in overall morbidity from 38.6% to 14.3%. This difference was primarily due to the primary outcome being a composite of treatment failure, readmissions and emergency consultations, and postoperative complications. There was a high rate of readmissions and emergency consultations in the DLC group (22.7%); the ELC group remained in the hospital before surgery and therefore did not have the opportunity to be readmitted preoperatively.
Secondary outcomes included conversion to open, biliary injury/leak, postoperative complications, total hospital length of stay, and total hospital costs. Duration of antibiotic therapy, total hospital length of stay, and costs were reduced with ELC. No statistically significant difference in conversion to open, biliary injury/leak, or postoperative complications was noted. Not all individual complications were collected. For example, no complications were reported relating to the longer duration of antibiotics with DLC such as Clostridium difficile colitis. The trial was only sufficiently powered to detect a large effect in overall morbidity (as defined above) and not for specific or even any 30-day complications. The authors note that more than 50,000 patients would have been required to identify a significant difference in bile duct injuries and leakage.
WHAT IS THE IMPACT OF CHANGE IN TRIAL DESIGN AND SAMPLE SIZE MIDWAY THROUGH THE TRIAL?
The trial was originally designed and powered to be a noninferiority trial with a sample size of 466 patients. At planned interim analysis after 50 patients, the trial was changed to be a superiority trial with a sample size of 86 patients, which was the final number of patients who were randomized. There are several differences between superiority and noninferiority trials, which are worth acknowledging. First, the null hypothesis for a superiority trial is that there is no difference between treatment arms. The null hypothesis for a noninferiority trial is that one treatment is worse than or inferior to another treatment based on a predefined margin. A noninferiority trial may be performed when a new treatment is perceived to have advantages over a more traditional treatment such as less harms or decreased costs.16
Second, superiority trials should be analyzed using an ITT analysis. On the contrary, noninferiority trials should be analyzed using both a per-protocol (PP) and an ITT analysis. In a PP analysis, patients are analyzed on the basis of the treatment they received. An ITT analysis may make the control treatment appear less effective due to noncompliance, which would result in the incorrect conclusion that a new treatment is noninferior. When both the ITT and the PP analysis yield similar results, then a conclusion of noninferiority is strengthened. As the trial by Roulin et al9 was revised to be a superiority trial, an ITT analysis was appropriate.
Another difference between superiority and noninferiority trials is in the sample size calculation. In a superiority trial, the sample size for a binary outcome is based on the acceptable error rates (α-false positive rate and β-false negative rate), the expected rate in the control group, and the hypothesized difference. Additional patients should be calculated based on the expected dropout rate. Usually, the sample size is based on a 2-sided test – that is, the new treatment could be better or worse than the control treatment. In a non-inferiority trial, the sample size is also based on acceptable error rates. However, the sample size is calculated based on the margin of difference between the 2 treatments – that is, that the new treatment is no worse than the control treatment by a specific margin. The sample size is based on a 1-sided confidence interval. Because the initial trial design was based on a very small noninferiority margin of 4%, the sample size was much larger. The modified sample size for the superiority trial hypothesized a 44% risk of overall morbidity in the DLC group and a 26% absolute reduction in the ELC group. As the observed effect was so large, there were no issues with power to detect a difference in the primary outcome.
CAN THE RESULTS BE APPLIED TO MY PATIENTS?
The trial by Roulin et al9 adds to the growing evidence that early cholecystectomy for acute cholecystitis results in less overall morbidity and decreased costs. Early cholecystectomy should be applied to acute cholecystitis patients who do not have severe sepsis or perforated cholecystitis, regardless of duration of symptoms. Although the trial was performed in Switzerland, the characteristics of the enrolled patients were similar to those of patients frequenting emergency centers in the US. Furthermore, in contrast to Swiss citizens who are required to have health insurance, many US citizens remain underinsured. Analyses of US databases demonstrate that there are significant disparities in the receipt of early, initial cholecystectomy among Medicaid patients resulting in increased costs and decreased success with a laparoscopic approach.17,18 Thus, widespread adoption of ELC could improve outcomes, reduce costs, and address known disparities.
Nonetheless, the lack of more rapid uptake of ELC for acute cholecystitis suggests that there are multiple barriers to the dissemination and implementation of the study results by Roulin et al.9 Notwithstanding the need to overcome surgical dogma and the ingrained practice of delaying cholecystectomy, other barriers include lack of operating room space or lack of time due to competing priorities of surgeons.19 Fortunately, with the advent of the acute care surgery model and with operating room time dedicated to these services, access and timeliness in many institutions are improving.20–22 Of note, Roulin et al9 observed that the majority of their procedures were performed within daytime hours. Although most studies of acute care surgery models have demonstrated an increase in daytime operating,23 this observation is relevant to all acute care and general surgeons and worthy of pause particularly, as studies comparing nighttime and daytime cholecystectomies have conflicting results.24–26 Acute cholecystitis after a prolonged period of symptoms can result in a gallbladder that is severely inflamed and contracted into the porta hepatis; this represents a potential hazard for a bile duct injury. Obtaining the “critical view” (anterior and posterior), performing a bile duct time out before transection, confirming regional anatomy [“BE-SAFE”: Bile duct, Enteric (ie, duodenum), Sulcus of rouviere, hepatic Artery, umbilical Fissure, and Environment [ie, back out the camera to provide a wide view)], and finally soliciting help from a trusted colleague are each paramount to ensuring safe surgery in the acute context.
In summary, ELC for acute cholecystitis regardless of duration of symptoms is supported by evidence as measured by patient, clinical, and resource-centered outcomes and should be adopted as standard of care. Future efforts should be focused on dissemination and implementation of this treatment strategy. Surgeon-level and organizational-level changes are needed in order to overcome the long-standing dogma of using 72 hours as a cut-off for delaying cholecystectomy.
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