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Anesthesiology:
Correspondence

Regional Techniques and Length of Hospital Stay after Abdominal Aortic Surgery

Norris, Edward J. M.D., M.B.A., F.A.H.A.*; Beattie, Charles M.D., Ph.D.

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In Reply:—
We thank Dr. Liu for his comments and interest in our clinical trial. 1 We agree that standardization of perioperative care may improve outcome and reduce length of stay (LOS) 2 and we addressed this concept in our manuscript. 1 This outcome benefit has been largely attributed to the reduction in the variation of clinical care. Our explicit and detailed perioperative clinical care protocols unquestionably reduced (and in some instances eliminated) variation in clinical care. However, our primary goal was not to reduce variation in care, but to optimize perioperative care in all treatment groups. Failure to optimize clinical care and postoperative pain relief in all treatment groups has significantly limited interpretation of clinical trials evaluating the role of anesthetic and analgesic techniques on outcome. Aggressive perioperative heart rate and blood pressure control, intensive physician-directed postoperative analgesia, and accelerated postoperative feeding and mobilization are several important aspects of our trial that both standardized and optimized clinical care. These features of our trial may have accelerated recovery and reduced perioperative morbidity, both of which could result in a LOS benefit regardless of anesthetic or analgesic technique. We observed an overall 31% reduction in mean LOS in our trial compared with historical controls at our institution (12.7 vs. 8.8 days). This rather marked reduction in LOS therefore made it unlikely that the hypothesized effect (2.5 day reduction in LOS) would be observed in any treatment group. Although some may argue that this invalidates our trial, we strongly argue to the contrary. If, as others have chosen to do, 3 we proceeded with a similar trial with only an epidural treatment group, one may have concluded (very inappropriately) that epidural anesthesia and analgesia dramatically reduced LOS and perioperative morbidity in patients undergoing aortic surgery.
We also agree that the Hawthorne effect is a potential limitation of all prospective clinical trials. It is currently not possible to determine when, and to what extent, this effect impacts a given trial. While it is certainly possible that caregivers and patients may have become more motivated to accelerate some aspects of postoperative recovery due to their awareness of our trial, the impact should have been similar in each of the treatment groups. Masking of both caregiver and patient to treatment assignment helped to insure that any Hawthorne effect, if present, was not treatment group specific. In addition, it is very unlikely that this effect had any significant impact on postoperative morbidity. Of particular note, median LOS for nonconsented (n = 123) and nonrandomized (n = 7) patients surviving to discharge was 8.0 days (range; 3–85) and 6.0 days (range; 6–10), respectively (Norris EJ, et al. unpublished data, 2001). These patients were not subjected to the rigors of our study protocols and epidural techniques were used in only two patients. We stand firmly behind the conclusions of our trial and believe they are both valid and important.
We appreciate the comments from Drs. Kehlet and Dahl. We agree that factors other than pain control impact on important perioperative outcomes. Indeed, that concept impacted significantly on the design of our previous clinical trial performed between 1988 and 1991. 4 In that trial we aggressively protocolized and optimized perioperative clinical care in both treatment groups. We introduced the use of rational blood pressure and heart rate control in an effort to reduce perioperative cardiac morbidity. These design features reduced the number of confounding variables and reduced the likelihood of unrevealed aspects of patient management impacting outcome. Subsequent work from our institution has demonstrated that factors such as organizational characteristics of intensive care units and nurse-to-patient ratios are associated with reduced LOS, lower hospital costs, and improved perioperative outcome. 5,6,7 We therefore contend that the conclusion of our trial—“in patients undergoing surgery of the abdominal aorta, thoracic epidural anesthesia combined with a light general anesthesia, and followed by either intravenous or epidural patient controlled analgesia, offers no major advantage or disadvantage when compared to general anesthesia alone followed by either intravenous or epidural patient controlled analgesia”—is very appropriate in 2001. We must disagree with Kehlet and Dahl's assertion that our trial utilized a “rather restrictive rehabilitation regimen.” On the contrary, our postoperative feeding and mobilization regimens were vastly accelerated compared with traditional postoperative care prior to the initiation of our trial. Furthermore, we do not believe that aortic surgery should be equated with colonic surgery. The analgesic regimens used in our trial were carefully developed and refined by experts in acute pain management and vascular anesthesia specifically for patients undergoing aortic reconstruction. Our goal was to optimize pain relief and minimize side effects while preserving postoperative masking. We believe that these goals were achieved with remarkable success. Patients randomized to epidural patient-controlled analgesia (PCA) received on average over 50% less opioid than patients randomized to intravenous PCA (Norris EJ, et al. unpublished data, 2001). Plasma fentanyl levels at 6, 24, and 48 h reflected this as well (Norris EJ, et al. unpublished data, 2001). These data are contrary to Kehlet and Dahl's suggestion that our epidural analgesia “merely reflected an epidural opioid regimen.” Since the conclusion of our trial, we have made continued efforts at our institution to accelerate recovery after aortic surgery. Median LOS for abdominal aortic surgery at our institution over the years 1998–2000 was 5.0 days (Norris EJ, et al. unpublished data, 2001). That LOS has been attained in the virtual absence of epidural techniques.
The comments of Clark et al. are appreciated. They offer the following question: “if postoperative pain scores are the same in all groups, how would one ever expect to see a difference in outcome?” We offer the following question in turn: “if perioperative care and pain relief are optimized and adverse outcomes minimized, is the analgesic technique even relevant?” Clark et al. are making the incorrect assumption that our epidural analgesia regimen resulted in suboptimal pain scores (relief). In our opinion, the more correct assumption is that pain scores were optimized in the intravenous analgesia regimen. Not optimizing pain relief in all treatment groups or comparing an “optimized” epidural regimen to a ‘suboptimal” opioid regimen are serious deficiencies of design. These deficiencies have plagued many previous studies 8–10 and are unfortunately present in two recent large-scale, randomized, clinical trials. 11,12 It is certainly possible that pain scores could have been improved in both our epidural and intravenous analgesic regimens, but not without increased (and unacceptable) side effects.
Dr. Andreae addresses concerns regarding our intraoperative use of “inadequate doses, regimen, and concentrations of local anesthetics.” He suggests that we may have “feared challenging episodes of hypotension,” and as a result reduced our epidural dosing to the extent that it invalidated our trial. As noted above with regard to our postoperative epidural analgesic regimen, our intraoperative epidural regimen was carefully developed and refined by anesthesiologists with extensive experience in aortic reconstruction. Our trial specifically included very high-risk patients requiring complex aortic reconstruction (25%) and high aortic cross-clamping (18%). “Fear” played no role in our study design or treatment protocols. Our intraoperative goals were to optimize all components of anesthesia, maintain appropriate hemodynamics, and preserve masking. This was accomplished with remarkable success. Our intraoperative epidural dosing is well described in our manuscript. 1 To summarize, we used 0.5% bupivicaine as a bolus and followed with a continuous infusion of 0.125% bupivicaine. Adjustments of the epidural infusion were made according to protocol. Of note, nearly two-thirds of patient with intraoperative epidural activation required at least one reduction in the infusion rate and a third of patients required two reductions (Norris EJ, et al. unpublished data, 2001), indicating an adequate level of epidural block. Only 15% of such patients required a single increase in their epidural infusion (Norris EJ, et al. unpublished data, 2001). Testing for adequacy of surgical blockade before induction of anesthesia was not planned because of the almost certain unmasking of both patient and treating physician. It has been our experience that if a bilateral (two or more segments) sensory block to pinprick is present after test dose administration via a thoracic epidural, the surgical block will be adequate with bolus dosing of 0.5% bupivicaine. Importantly, there was no evidence of inadequate intraoperative anesthesia in any patient. Finally, it is noteworthy that Andreae seems unconcerned about the adequacy or appropriateness of the “systemic analgesic” regimens used in the meta-analysis trials as reported by W.S. Beattie. 13 Few, if any, of the meta-analysis trials actually used carefully administered intravenous PCA postoperatively. We believe that intravenous PCA is the only legitimate analgesic modality for the control group of any modern-day study evaluating epidural analgesia.
Karanikolas et al. question our choice of LOS as a primary outcome variable. Our rational for using LOS was addressed in our manuscript and we maintain that LOS is a relevant health outcome important to patients, payers, and society. We agree that LOS can be affected by many factors and that is why we rigorously protocolized perioperative medical management, standardized postoperative surgical care, optimized pain relief, and stratified patients by surgeon. We used opioids in our epidural regimens because combination therapy clearly improves pain control and minimizes side effects. A more aggressive multimodal postoperative program may have further reduced LOS, but this would have most likely occurred to a similar extend in all treatment groups. For example, there is little to suggest that the addition of acetaminophen, ibuprofen, and ketorolac to improve postoperative pain would have impacted outcome to a greater extent in one analgesic group over the other.
Karanikolas et al. states that a “growing body of evidence shows that the use of epidural anesthesia and analgesia is beneficial.” Our question is, “compared to what?” The historical studies which form the basis of the recent meta-analysis reviews, 13,14 as well as those currently being published, 12 have neglected to control, specify, and optimize treatment in the nonepidural wings of their studies. Why is this? Do investigators really think all forms of “parenteral analgesia” are equivalent? Are reimbursement issues at play? Are political or jurisdictional forces preventing proper study design? Are regional enthusiasts with no interest in the nonepidural modalities conducting the studies? The successful prosecution of our study required the cooperation of anesthesiologists, surgeons, internists, ICU nursing, ward nursing, and pain team members. Thus, we were able to institute intravenous PCA in all patients who randomized to that treatment. Investigations will continue to show that epidural techniques outperform: (1) poorly conducted general anesthesia; (2) general anesthesia with higher than normal death or complication rates; and (3) uncontrolled and sub-optimal postoperative pain management in the nonepidural wing. Karanikolas et al. conclude with a “caution against the more general interpretation that epidural anesthesia–analgesia is not beneficial.” We agree with that caution, and for the reasons cited above, would add “caution against the more general interpretation that epidural anesthesia–analgesia is beneficial.”
The comments from Drs. Heid and Jage are appreciated. We too were somewhat surprised that our epidural analgesic regimen did not result in superior (dynamic) pain scores. Our intensive, physician-directed, acute pain service's goal was to optimize pain relief in all patients. This service evaluated patients on arrival to the intensive care unit, at 2 and 6 h after intensive care unit arrival, three times daily for the first 3 postoperative days, and daily through postoperative day 7. The acute pain attending was available for consultation at all times and a member of the pain service was available on-site for patient evaluation 24 h a day. It may therefore not be a complete surprise that both analgesic regimens resulted in good pain control and similar pain scores. Importantly, optimization of pain control was done in a double-masked setting, as was the evaluation of pain scores. Investigator bias has no doubt had a very significant impact on many clinical trials evaluating analgesic techniques. Efforts to eliminate bias and optimize care are important aspects of our study design that need to be incorporated in future trials. Fentanyl consumption in the intravenous PCA group averaged approximately 75 μg/h for the first 36 h period and approximately 45 μg/h for the second 36 h period (Norris EJ, et al. unpublished data, 2001). In the epidural PCA group, consumption was approximately 35 μg/h and approximately 20 μg/h for the first and second 36 h periods, respectively (Norris EJ, et al. unpublished data, 2001). Side effects were generally mild and easily managed.
Bacchetti and Leung address concerns regarding the use of sample size and power calculations and promote the reporting of confidence intervals. We agree that confidence intervals are useful, and that is why we presented them for LOS—the design variable (primary outcome) of our trial. 1 Sample size data were presented to indicate the planned approach to our study design, not to “help” in interpretation of results as suggested by Bacchetti and Leung. It would not be prudent to undertake a fixed sample size trial without a sample size calculation to determine the number of patients required or the power available with a specified sample size. Furthermore, we believe it would have been unethical to initiate our trial and expect patients to accept the risks, however small, of our double-masked treatment protocols (including a sham epidural) without first establishing study design features and sample size requirements. With regard to a priori calculations, they are all based on assumptions or wishful thinking. So what? No one says that the assumptions made in sample size calculations must hold. Bacchetti and Leung's assertion that “perhaps the worst aspect of reporting sample size or power calculations is that it encourages interpretation of studies’ results based only on P values, in particular the widespread fallacy of interpreting P > 0.05 as proving the null hypothesis” is absurd. Sample size is sample size. When designing a clinical trial some goal must guide the study population size. Bacchetti and Leung seem unaware of that fact. What method to determine sample size would they suggest? Post hoc power calculations are also important and should be part of all manuscripts where the observed treatment effect is small and the authors conclude in favor of the null hypothesis, that is, no difference among treatment groups. These calculations are frequently helpful to the reader when attempting to determine whether to accept the author's conclusions. In addition, the post hoc conditional power analysis helped inform our clinical trial monitoring committee's decision to terminate the trial. Finally, there is unfortunately no protection against “unsophisticated readers.” Such readers are just as likely to misinterpret aspects of Bacchetti and Leung's letter—“the exact 95% confidence interval around the odds ratio for death comparing intravenous versus epidural postoperative analgesia goes from 0.36 to 5.4” and “the presence of outliers would require a bootstrapping method to obtain a valid confidence interval for a difference in means.”
Finally, we thank Dr. Amar for his comments and interest in our clinical trial. 1 He is correct that our study was not powered to detect differences among or between treatment groups with regard to cardiovascular outcomes. However, that is not a “limitation” of our trial. Our study question and design were clearly articulated in our manuscript. The trial was powered for LOS, not cardiovascular outcomes. We reported in our Results that ‘hospital mortality, cardiac death, and mortality at 12 months were not different among the four treatment groups,” and with regard to major (cardiac) morbidity, “no significant difference was observed among the four treatment groups.” These are an accurate characterization of what was observed in our trial. Although the casual reader of only our abstract may very well misinterpret, “postoperative outcomes were similar among the four treatment groups with respect to death, myocardial infarction,” the conscientious reader of the entire manuscript will not.
In summary, we appreciate the opportunity to respond to all of these letters and thank all of the contributors for their comments and interest in our trial.
Edward J. Norris, M.D., M.B.A., F.A.H.A.*
Charles Beattie, M.D., Ph.D.
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References

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