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Annals of Surgery Journal Club
Interactive resource for surgery residents and surgeons to discuss and critically evaluate articles published in Annals of Surgery selected by a monthly guest expert who will review an article each month, offer questions and respond to reader's comments.
Wednesday, July 01, 2015

Moderator: Thomas H. Cogbill, M.D.

Paquette IM, Zuckerman R, Finlayson SRG: Perforated appendicitis among rural and urban patients: implications of access to care. Ann Surg. 2011;253:534-538.

In this retrospective cohort study, the authors used the 2003-2004 National Inpatient Sample to collect data on 122,990 patients with acute appendicitis. Using urban influence codes provided by the United States Department of Agriculture, 7597 patients were classified as rural and 103,801 patients as urban. These two groups were compared by univariate and multivariate analysis.

The overall rate of perforated appendicitis was 32%. Patients with perforation had mean hospital lengths of stay 3.6 days longer and incurred mean charges of $5714 more per patient than those without perforation. The rate of perforation was 35.8% in rural patients and 31.5% in urban patients (p 40 years, male gender, transfer from another facility, black race, poorest 25 percentiles, Charlson comorbidity score >= 3, and rural residence. Logistic regression was used to demonstrate that the difference in perforation rates between rural and urban patients persisted when other factors associated with perforation were controlled.

Nearly 98% of urban patients were discharged from an urban hospital and 30% of rural patients were discharged from an urban hospital. Rural patients discharged from urban hospitals were more likely than rural patients discharged from rural hospitals to have a diagnosis of perforation (OR = 1.23).

The authors concluded that patients from rural areas have higher rates of perforation associated with acute appendicitis than their urban counterparts. They opined that this difference suggests a disparity in access to timely surgical care and is the result of geographic, provider, and/or patient factors.

About the Author

Dr. Thomas H. Cogbill  received his MD from the University of Colorado in 1977 and completed surgical residency at the University of Colorado Medical Center in 1982.  He has practiced general surgery at Gundersen Health System in La Crosse WI from 1982 to present.   He was the Program Director of the general surgery residency at Gundersen Medical Foundation from 1990-2010..  He is a Clinical Professor of Surgery at the University of Wisconsin School of Medicine and Public Health.  Dr. Cogbill was the Chair of the American Board of Surgery in 2012-2013.  His research interests include general surgery workforce, general surgery education, trauma, and rural surgery.


  1. Could selection bias have accounted for some of the difference in the rates of perforated appendicitis in rural patients treated at urban versus rural hospitals? Is it possible that rural patients with perforated appendicitis and abscess might have been transferred to urban hospitals for percutaneous drainage by interventional radiologists? Is it likely that rural patients with sepsis and multiple system organ failure due to perforated appendicitis required transfer to urban hospitals for critical care management? How could the authors have investigated the magnitude of these effects?
  2. Many rural U.S. counties have Critical Access Hospitals (CAH). One of the stipulations for CAH designation is adherence to the 96 hour rule. This rule states a) the CAH is required to assure that acute inpatient care does not exceed 96 hours on average per patient and b) the CAH will only receive payment if a physician certifies that a patient being admitted is expected to be discharged or transferred to another institution within 96 hours. Could application of this rule have caused more rural patients with perforated appendicitis ( with longer expected length of stay ) to be transferred to urban hospitals?
  3. There are three common situations in rural U.S. counties : a) No hospital and no general surgeon(s) are in the county, b) A hospital but no general surgeon(s) are in the county, and c) Both a hospital and a general surgeon(s)are in the county. Are there possible differences in the rates of perforation in residents of these county classifications? Are the barriers to access of health care different in each of the three different settings above? How might these differences influence potential solutions in each of these three settings? Does the presence of a general surgeon in a rural county result in lower rates of perforated appendicitis in that county's residents?
  4. Several authors have recently proposed that early appendicitis can be safely managed with antibiotics alone. If this trend were to expand, how might the disparity in rates of perforated appendicitis between rural and urban areas be affected? Who would follow rural patients treated nonoperatively?
  5. The authors concluded that the increased rate of perforated appendicitis in residents of the rural U.S. was due to geographic, patient, and/or provider factors. What strategies might be used to alleviate obstacles in each of these three categories?
  6. Currently, the most serious surgical workforce shortage in the U.S. concerns general surgeons in rural areas. The shortage is forecast to worsen over the next 20 years. What strategies might be used to provide incentive for general surgeons to practice in rural areas?

Monday, June 01, 2015

Moderator: Paul E. Wise, M.D.

Vather R, Josephson R, Jaung R, et al. Gastrografin in Prolonged Postoperative Ileus--A Double-blinded Randomized Controlled Trial. Ann Surg. 2015 Jan 8. [Epub ahead of print].

In this trial from New Zealand conducted between September 2012 and June 2014, the authors performed a double-blinded, randomized, placebo-controlled study in 80 patients comparing a one-time dose of Gastrografin (an orally administered, water-soluble, hyperosmolar agent) versus a control agent (an anise oil, ethanol, glycerol mixture) to resolve prolonged post-operative ileus (PPOI) after elective colorectal operations. Well-defined criteria were used to determine the presence of PPOI and resolution of PPOI, and they followed the patients prospectively to assess the primary endpoint of duration of PPOI (time from diagnosis to resolution of PPOI) and the secondary endpoints of time until discharge criteria were met, length of stay (LOS), and readmission. The authors found that the mean duration of PPOI did not differ between the groups (83.7 vs 101.3 hours; P=0.191) despite an "accelerated time to flatus or stool (18.9 vs 32.7 hours; P = 0.047) and time to resolution of abdominal distension (52.8 vs 77.7 hours; P = 0.013)." There were no differences in complications, readmission, or LOS (10 days vs 13 days; p=0.262). The authors concluded that "Gastrografin is not clinically useful in shortening an episode of PPOI characterized by upper and lower gastrointestinal symptoms."

About the Author

Dr. Paul E. Wise is an Associate Professor of Surgery at Washington University in St. Louis School of Medicine where he serves as Program Director of the General Surgery Residency and Director of the Inherited Colorectal Cancer and Polyposis Registry. He completed his General Surgery residency at Vanderbilt University Medical Center in Nashville and his colon and rectal surgery fellowship at Washington University in St, Louis/Barnes Jewish Hospital after completing medical school at Johns Hopkins University School of Medicine in 1996. He has been a Council member as well as President of the Collaborative Group of the Americas on Inherited Colorectal Cancer and is a member of multiple committees in the American Society of Colon and Rectal Surgeons and the Society of Surgeons of the Alimentary Tract. His research interests include hereditary colorectal cancer syndromes, improving outcomes after colorectal surgery, and surgical education.


  1. The sample size for the study of 80 patients was determined based on a PPOI incidence at their institution of almost 20% and lasting 4.5 days (Vather R, Bissett IP. Int J Colorectal Dis. 2013;28(10):1385-91). To calculate their sample size, the authors anticipated a 33% shorter duration of PPOI with Gastrografin. Does this seem like a reasonable means to determine the number of patients needed to avoid a type II error (failure to reject the null hypothesis)?
  2. The authors point out in the Discussion that defining the types of ileus may impact the possible therapeutic measures employed to help the PPOI resolve, if any. With less than 50% of the patients in this study showing "hard" signs of ileus (cessation of bowel function/flatus and/or radiographic findings), did the authors select a patient group less likely to benefit from the intervention? If so, would their numbers likely allow a subgroup analysis of the effectiveness of Gastrografin for those patients with "hard" signs/"lower GI symptoms"?
  3. Should the authors have included patients with ostomies in the cohort? If not, why not?
  4. The authors have noted factors that impact development of PPOI (Vather R, et al. Surgery. 2015;157(4):764-73). Should the authors have used any of these criteria for the randomization?
  5. Should the authors ensure (or at least report) their protocol for post-operative care in terms of early ambulation or other interventions known to impact development, and potentially duration, of PPOI? Would the randomization necessarily negate the need to report these factors?
  6. Does the increased use of opiates in the Gastrografin group impact the results, and if so, how?
  7. How are the author's endpoints potentially impacted by the clinicians' rounding and ordering habits? Might this impact time to consumption of oral diet and/or discharge timing/LOS, for example?

Friday, May 01, 2015

Moderator: Ronald B. Hirschl, MD

Russell KW, Rollins MD, Barnhart DC, et al. Charge Awareness Affects Treatment Choice: Prospective Randomized Trial in Pediatric Appendectomy. Ann Surg. 2014 Sep 1. [Epub ahead of print]

Summary: 100 non-obese patients and families with non-complicated appendicitis were shown a video explaining what appendicitis is, the open and laparoscopic techniques, and the advantages/ disadvantages of the two approaches. Approximately half of the patients (n=49) were randomized to see a video that contained information revealing that the charges associated with an open appendectomy was $160 whereas those associated with a laparoscopic appendectomy was $2172. The charge information was absent in the video shown to the second group (n=51). Those exposed to such charge data were significantly more likely to choose open versus laparoscopic appendectomy (open appendectomy: charge exposure group = 63%, those not exposed to charge data = 35%). The group exposed to charge information made decisions which saved $528 per patient. 90% of patients appreciated being offered a choice in their medical care.

The following questions are worthwhile to consider:

  1. The authors suggest that there is equipoise between laparoscopic and open appendectomy. Is this true given that studies suggest that as of 2011-12 there is a strong and steady increasing 2-decade trend toward the laparoscopic approach to appendectomy with residents now performing ~70% of appendectomies via a laparoscopic approach? Does the surgeon's preference or even comfort level with one approach or another play a role in the decision of which approach is used? What would you personally do if a parent suggested that they wanted an open instead of a laparoscopic appendectomy because they had a high deductible and it was cheaper?
  2. Is there significant bias introduced in this study? Since it is stated in the video that “the cost of healthcare is a national problem” followed by provision of charge data, might a parent be more likely to choose the less costly approach?
  3. Would you as a surgeon alter your choice of approach if you knew the charge or cost differences? What if you shared in the cost savings or your salary was linked to an increase in costs: would that alter your approach?
  4. How would you recommend a patient/family or surgeon incorporate the variables that were not assessed in this study into their decision-making regarding which approach to use: length of stay, pain level, cosmesis?


  1. Richards MK, McAteer JP, Drake FT, Goldin AB, Khandelwal S, Gow KW. A national review of the frequency of minimally invasive surgery among general surgery residents: assessment of ACGME case logs during 2 decades of general surgery resident training. JAMA Surg. 2015;150:169-172.
  2. McCoy, AC, Gasevic, E,Szlabick, R, Sahmoun, AE, Sticca, RP. Are Open Abdominal Procedures a Thing of the Past? An Analysis of Graduating General Surgery Residents’ Case Logs From 2000 to 2011. J Surg Ed. 2013;70:683-689.

Wednesday, April 01, 2015

Moderator: Mary T. Hawn, MD

Kasotakis G, Lakha A, Sarkar B, et al. Trainee participation is associated with adverse outcomes in emergency general surgery: an analysis of the National Surgical Quality Improvement Program database.Ann Surg. 2014;260:483-493.

Kasotakis and colleagues attempt to define whether surgical trainee participation in emergency general surgery cases results in adverse outcomes. They use the American College of Surgeons National Surgical Quality Improvement Program (NSQIP) data to asses the effect o trainee participation. They matched procedures with and without trainee participation and found that when a trainee was involved, nearly all adverse outcomes measured occurred at a higher frequency. They suggest that much of this may be mediated through the increased operative time associated with resident participation in an operation.

In my opinion, this paper has two major flaws. First, given that no hospital identifiers are provided in the NSQIP participant use file, there is no ability to control for the hospital level effect on post-operative outcomes. Second, the authors made no effort to exclude patients that were transferred to a hospital from a dataset. It is my experience that complicated procedures such as obstructing cancers, multiply recurrent hernias with loss of domain and cholecystitis in the setting of cirrhosis are much more likely to be transferred to a tertiary referral center rather than being managed at a community hospital. While the authors did control for the differences in comorbid conditions that are observed in tertiary care hospitals, there is little ability to control for the challenging surgical presentation that often results in transfer to a higher level of care because of the known attendant higher rates of adverse outcomes.

I would caution any conclusions being drawn from the data presented in this paper. A previous publication from the College found that trainee participation was not associated with adverse outcomes (Ravel et al, J Am Coll Surg. 2011;212:889–898). The investigators at the ACS are able to control for hospital level variation and produce more reliable findings.


  1. Trainee participation in emergency surgical procedures is vitally important for comprehensive surgical training. Based on the findings in this study, should the potential harm from resident participation in an emergency case be addressed in the informed consent?
  2. Given that healthcare reform has placed increasing emphasis on transparence in outcomes and quality, what are potential consequences for academic training programs from this study?
  3. The authors suggest that the potential increase in harm comes from trainee participation, however, could this be a surrogate for the quality of care provided by attending surgeons or academic medical centers?

Tuesday, March 03, 2015

Moderator: Ali Salim, MD

Minei JP, Fabian TC, Guffey DM, et al. Increased trauma center volume is associated with improved survival after severe injury. Ann Surg. 2014;260:456-465.

There has been a long-standing debate on the hospital factors that influence better patient outcomes among trauma centers. While some studies indicate that larger volume centers have better outcomes, others have shown that higher trauma center designation, not volume, predicts better outcomes. Because many previous studies have collected either retrospective clinical data or administrative data with limited clinical information, the authors of this paper decided to use a prospectively collected clinical database to show the relationship between trauma center volume and patient outcomes.

The study was a secondary analysis of two completed randomized controlled clinical trials performed by the Resuscitation Outcomes Consortium: one enrolling patients that had hypovolemic shock and the other enrolling patients with severe traumatic brain injury (TBI). In both trials, the interventions were in three arms: pre-hospital hypertonic saline, hypertonic saline with 6% dextran 70, or normal saline. For this study, the patients were analyzed based on the hospitals they were admitted to. Trauma center volume was categorized as annual patient volume in increments of 1000 and trauma center designation was categorized as Level I or Level II. The primary outcomes were 24-hour and 28-day mortality, while secondary outcomes that measured hospital events and long-term functional outcomes were also analyzed. Variables that measured injury severity, pre-hospital care, and admission physiology were recorded. Various models were used to identify hospital factors that predict better outcomes while adjusting for potential confounders.

After adjusting for potential confounders, there was no difference in 24-hour mortality in either the shock cohort or the TBI cohort based on trauma center designation or volume. Analyzing all the patients together, however, showed that increased volume was associated with lower 24-hour mortality. A similar analysis of 28-day mortality showed the same association when all patients were combined. But this association only persisted in the TBI cohort on stratified analysis. Interestingly, Level I trauma center status was associated with reduced 28-day mortality in the shock cohort even after adjusting for hospital volume. When other secondary outcomes such as ventilator-free days and Multiple Organ Dysfunction were analyzed, higher volume seemed to predict better outcomes. However, higher volume centers had higher complication rates. Trauma center status did not seem to influence outcomes significantly.

The strengths of this study include the detail of clinical information that was collected prospectively, the long-term follow up of patients and the careful selection of patients. However, some limitations exist. Although the different arms of treatment in the original randomized trial were associated with different risks of mortality, the authors did not consider treatment arms in the analyses. In addition, only 11 centers were included in the study and individual hospital factors aside from volume and trauma center designation could easily bias the results of the study even after accounting for within-hospital correlation. The authors concluded that higher volume centers are more likely to have better systems to provide trauma care. Therefore, to optimize outcomes in patients with severe injuries, they should preferentially be taken to higher volume centers.


  1. Based on the results of this study, should hospitals focus on increasing their volume instead of improving their practices and procedures?
  2. 2.
  3. If the protocols demand directing severe injuries to higher volume centers, is there a potential for these centers to get overwhelmed by the volume of patients? In other words, is there a maximum volume threshold for improved outcomes?
  4. 3.
  5. Would adjusting for other hospital factors have changed the results?
  6. 4.
  7. How generalizable are the results? The practices and procedures involved, within the included trauma centers, to perform a high quality parallel randomized prospective trial may not be applicable to other trauma centers.