Beidas, Sary O. LTC MC
To the Editor:
In 2005, the American Thoracic Society/Infectious Diseases Society of America (ATS/IDSA) guidelines for management of nosocomial pneumonia recommended a shortened course (8 days) for the treatment of nonpseudomonas ventilator-associated pneumonia (VAP).1 These recommendations for a shortened antibiotic course were based on a study by Chastre et al,2 published in 2003. The ATS/IDSA guideline panel reviewers ranked the study as a level 1 evidence-based trial. This commentary was initiated to determine if the study outcomes and recommendations may be generalized to patients with VAP as described in the ATS/IDSA guidelines.
I describe some of the issues related to the study and provide the rationale for revising the recommendation for listing the study by Chastre et al from a level 1 to a level 2 evidence-based grade in the ATS/IDSA guideline for managing patients with nosocomial pneumonia. Unless the ATS/IDSA revised their level 1 to level 2 evidence-based grade, physicians may treat patients with nosocomial pneumonias for shorter durations of time, which may result in potentially negative patient outcomes. This is especially relevant because nosocomial pneumonia is the leading cause of infection and a major contributor to mortality in intensive care units (ICUs).
The guidelines used by ATS/IDSA for evidence-based grading incorporate a 3-level tiered approach. A level 1 study as defined by the ATS/IDSA guidelines states that the "Evidence comes from well-conducted, randomized controlled trials," and for level-2 studies, "Evidence from well-designed, controlled trials without randomization."1 For a standardized nomenclature on randomization and double-blinding, the reader is advised to see the revised CONSORT statement.3
The study by Chastre et al was designed as a randomized, double-blind trial to treat a selective group of patients with late-onset VAP. On day 1 of the study, bronchoscopy was performed on the patients, and antibiotics were administered. Randomization and blinding of patients followed on day 3, with the double-blind ending on day 8 (double-blinding occurred during one third of the time on-therapy). Investigators in this multicenter trial used the initial 3 days on-therapy to decide whether patients would continue in the trial or be designated ineligible to continue in the study. Treating physicians were permitted a broad latitude in antibiotic selection (a β-lactam combined with a fluoroquinolone or an aminoglycoside).
Point: The reason for randomization and blinding is to circumvent the problem of selection bias. A delay in randomization of patients to the third day on-therapy allows the investigators to continue or exclude patients in the study based on their clinical response. However, when physicians are permitted to observe patients' clinical response before randomization and blinding, there is an increased chance for selecting patients that may influence patient outcomes to a particular treatment group. In addition, the study report does not address allocation concealment. To give credit to the study authors, they do state that they intentionally choose a well-defined select group of ICU patients with confirmed VAP.
As noted in the study, 66% (769/1171) of patients assessed for the study were ineligible. These patients were systematically excluded over the course of 3 days. A partial list of reasons for ineligibility criteria included early-onset pneumonia, Simplified Acute Physiology Score II score more than 65, death before day 3, and immunocompromised status.
Point: Other less well-documented reasons for ineligibility included inappropriate empirical antibiotic treatment and exclusions for other reasons. These later 2 categories of ineligibility included a substantial number of patients (140 patients). How can we ascertain that the ineligibility of these patient subsets did not affect the outcome results in this study in favor of the 8-day course? The issue of eligibility runs in parallel to the prior point where investigators were allowed to observe treatment effects before randomization and blinding.
Another issue of concern in the study is the lack of a standardized empiric antibiotic regimen. In general, investigators prescribed antibiotics based on a general framework which allowed significant variability between the treatment sites. The protocol specified that antibiotic regimens should preferably include a β-lactam combined with a fluoroquinolone or an aminoglycoside. On day 1 of the study, more than 90% of the patients in both groups received equivalent antibiotic agents as specified in the study report; by day 8 of the study, these numbers were down to 33% of patients in the 8-day treatment group and 39% of patients in the 15-day treatment group.
Point: This variability in empiric treatment combined with delayed randomization and double-blinding increases the likelihood of introducing serious confounders related to therapeutic regimens. β-Lactams and fluoroquinolones belong to 2 different classes of antimicrobials. Within each class, the individual agents are not necessarily mutually interchangeable (in contrast to aminoglycosides). In addition, bacterial resistance and sensitivity patterns vary within hospitals. The rates and variety for antimicrobials provided in the study do not provide reassurances that therapy was standardized between the 2 groups; if anything, the antibiotic use rates from day 1 through day 8 suggest extreme variability within the selected treatment regimens.
Similarly, vancomycin was used on day 1 of the study in 39% of patients in the 8-day treatment group and 37% of patients in the 15-day treatment group. Ventilator-associated pneumonia rates for Staphylococcus aureus in the study were 20.6% (65 patients) and 19% (60 patients) in the 8- and 15-day groups, respectively. Interestingly, the relapse rate for patients with methicillin-resistant S. aureus was higher in the 15-day treatment group.
Point: Several questions arise regarding the use of vancomycin in the study. For example: Should empiric therapy regimens for late VAP routinely include vancomycin? Were any of the patients in the study treated with antibiotics active against MRSA? How did the investigators decide who to treat for Staphylococcus infection at enrollment? These questions are especially relevant because the rate of MRSA superinfection and recurrence is higher in the 15-day treatment group; this is an unexpected result. Is there something different in the demographic characteristics of either group that could have led to the difference in MRSA relapse rates? The authors could have provided us with a plausible explanation for these unexpected and higher MRSA relapse rates in the 15-day treatment group.
Overall, relapse rates in all patients were 16.8% (33/197 patients) in the 8-day treatment group and 11.3% (23/204 patients) in the 15-day treatment group; these differences were statistically significant according to the defined 90% confidence interval for the between-group risk difference of 5.5% (0.7%-10.3%). Relapse rates for nonfermenting gram-negative organisms were higher for the 8-day treatment group (32.8% [21/64 patients]) compared with (19% [12/63 patients]) the 15-day treatment group.
Point: We expect nonfermenting gram-negative organisms and MRSA to require more intensive and prolonged antimicrobial therapy. In regard to the former organisms, the higher rates of relapse are in line with our expectations; however, for MRSA relapses, the study confounders already mentioned limit further inferential exploration. This unexpected result for MRSA relapse in the 15-day treatment group is likely to have skewed the results in favor of the 8-day treatment course achieving parity with the 15-day treatment course.
The study lists 3 primary end points: total deaths, recurrence of infection, and antibiotic free days.
Point: Because this was a noninferiority study, the authors could have identified 1 primary end point (eg, "success" or "failure"), supported by multiple secondary end points. In this complex population with poorly defined physiological abnormalities, the primary end point of death due to any cause measured at 28 days lacks precision. Hence, the Kaplan-Meier estimate for the probability of survival does not provide sufficient reassurance that the 8-day antibiotic treatment course was noninferior to the 15-day treatment course.4,5 One has to question the reliability of using all-cause death as an end point in ICU patients. Should we accept a simple intervention such as shortening an antibiotic course to impact mortality in a complex population with poorly defined physiological abnormalities? Even if it does, that would require a large population sample and histopathology confirmation of VAP because mortality is a poor discriminator for causality in this population. Two good examples for studies using patient outcomes instead of mortality as the primary outcome in VAP were published.6,7 Both studies were used in regulatory approval for indications specific to nosocomial pneumonia. In these studies, clinical and microbiological outcomes were the primary measures for response; death was a secondary outcome.
The authors emphasize in the discussion section that the study's unblinded design may have contributed to the level of uncertainty surrounding the potential effect favoring the shortened 8-day treatment course. Another major limitation identified by the authors was the high rate for exclusion of patients who did not meet the study's defined narrow inclusion criteria. Therefore, the generalizability of the results of this study to the overall population of nosocomial pneumonia is limited to a small select population. Had the investigators standardized the empiric treatment at all centers and randomized patients at the outset using a true double-blind protocol, the results of the study would have been more credible.
An underlying assumption in the study was the necessary use of bronchoalveolar lavage or protected specimen brush for confirming a diagnosis of VAP. However, as described in the ATS/IDSA guidelines, one of the vexing problems with all studies of nosocomial pneumonia is absence of a "gold standard."1 Hence, the closest we may get in terms of a gold standard for diagnosing VAP is the recent report by Klompas, which describes clinical findings associated in patients with VAP who have histological tissue obtained by pulmonary biopsy or at autopsy confirming nosocomial pneumonia. Even then, his study is beset by its own limitations due to the severity of illness included in the analysis and the small numbers of cases described in each study reviewed.8 Other studies published since the guidelines in 2005 question the validity for obtaining bronchoscopy samples for diagnosis in all cases of VAP and suggest that nonquantitative endotracheal specimens may be just as reliable.9
In conclusion, we recommend the ATS/IDSA committee to revise the evidence-based level grade applied to the study by Chastre and colleagues from level 1 to level 2, to ensure patient safety and adequate treatment for patients with VAP. Until clinical trials designed to study the duration of therapy for nosocomial pneumonia can select reliable and valid end points and study patients in a true randomized, double-blinded fashion, we should continue treating patients with nosocomial pneumonia using the time-honored 14- to 21-day antibiotic regimen.
Sary O. Beidas, LTC MC
Infectious Diseases Service
Walter Reed Army Medical Center
1. Guidelines for the management of adults with hospital-acquired, ventilator-associated, and healthcare-associated pneumonia. Am J Respir Crit Care Med. 2005;171:388-416.
2. Chastre J, Wolf M, Fagon JY, et al. Comparison of 8 vs 15 days of antibiotic therapy for ventilator-associated pneumonia in adults. JAMA. 2003;290(19):2588-2598.
3. Altman D, Schulz KF, Moher D, et al. The revised CONSORT statement for reporting randomized trials: explanation and elaboration. Ann Intern Med. 2001;134:663-694.
4. Hébert PC, Cook DJ, Wells G, et al. The design of randomized clinical trials in critically ill patients. Chest. 2002;121:1290-1300.
5. Petros AJ, Marshall JC, van Saene HKF. Should morbidity replace mortality as an endpoint for clinical trials in intensive care? Lancet. 1995;345:369-371.
6. West M, Boulanger BR, Fogarty C, et al. Levofloxacin compared with imipenem/cilastatin followed by ciprofloxacin in adult patients with nosocomial pneumonia: a multicenter, prospective, randomized, open-label study. Clinical Therapeutics. 2003;25(2):485-506.
7. Rubinstein E, Cammarata SK, Oliphant TH, et al. Linezolid versus vancomycin in the treatment of hospitalized patients with nosocomial pneumonia: a randomized, double-blind, multicenter study. Clin Infect Dis. 2001;32:402-412.
8. Klompas M. Does this patient have ventilator-associated pneumonia? JAMA. 2007;297:1583-1593.
9. The Canadian Critical Care Trials Group. A randomized trial of diagnostic techniques for ventilator-associated pneumonia. N Engl J Med. 2006;355:2619-2630.
© 2008 Lippincott Williams & Wilkins, Inc.