prophylaxis that they are receiving or dissatisfied with the clinical expertise of the physicians providing postex- posure prophylaxis. In these cases, there were superb 24-hour resources staffed by trained personnel in postex- posure prophylaxis.

The National Clinicians’ Post-Exposure Prophylaxis Hotline (PEPline, 888-448-4911) is a unique resource for emergency medical and operating room personnel who have questions about postexposure prophylaxis. The program is conducted by the University of California-San Francisco/San Francisco General Hospital staff. This program receives support from the Health Resources and Services Administration Ryan White CARE Act, the HIV/ AIDS Bureau, the AIDS Education and Training Centers, and the Centers for Disease Control and Prevention. Its Web site has a link to the updated Compendium of State HIV testing Laws. This service also has a link to a valuable Web site (http://www.cdc.gov/hepatitis/). The authors of this Editorial were shocked to learn that this extremely valuable PEPline is temporarily unavailable to provide live hotline consultations between 11:00 PM and 6:00 AM Pacific Standard Time.

The Compendium of State HIV Testing Laws describes key State HIV testing laws and policies. Each State’s HIV testing laws are unique, and many have undergone revision or supplementation since the release of the Centers for Disease Control and Prevention’s 2006 HIV testing recommendations. The Compendium is designed to help clinicians understand HIV testing laws and to implement sound HIV testing policies. It should not, however, be used as an official legal document.

The National Clinicians’ Consultation Center provides clinical consultation for health care providers as part of the Health Resources and Services Administration AIDS Education and Training Centers program. Clinicians with questions about HIV testing are encouraged to call the National HIV Telephone Consultation Service (Warmline) at (800) 933-3413. The Warmline also provides advice on HIV management, including antiretroviral treatment.

With a growing number of patients without health insurance receiving care in emergency departments (ED) and trauma centers, it has been very difficult for many hospitals in our country to get adequate numbers of ED personnel as well as trauma center staff. Because it has been our goal to ensure that our staff receives optimal postexposure prophylaxis against blood-borne viral infec- tions, we have routinely sought the advice of the National Clinicians Post-Exposure Prophylaxis Hotline 24 hours a day regarding the prevention, diagnosis, and treatment of blood-borne viral infections. Because this superb service does not have adequate funding to respond to PEPline telephone calls 24 hours a day, we are concerned that the ED and trauma center staff will not be receiving optimal guidance in the prevention and treatment of blood-borne viral infections. Consequently, we have written a letter to President Obama requesting

additional Federal funding for the PEPline service that will allow its superb staff to answer PEPline calls 24 hours a day. This is our quest!

Richard F. Edlich MD, PhD Biomedical Engineering and Emergency Medicine

University of Virginia Health System

Charlottesville, VA, USA E-mail address: [email protected]

Jamie J. Clark Holly S. Stevens Jill J. Dahlstrom

Research Assistants to Dr. Edlich Brush Prairie, WA, USA

K. Dean Gubler DO, MPH

Legacy Emanuel Medical Center

Portland, OR, USA

Willam B. Long III MD

Legacy Emanuel Medical Center

Portland, OR, USA

doi:10.1016/j.ajem.2010.06.023

Reference

[1] Edlich RF, Wind TC, Heather CL, Degnan GG, Drake BB. Recommendations for postexposure prophylaxis of operating room personnel and patients exposed to bloodborne diseases. J Long Term Eff Med Implants 2003;13:103-6.

The AutoPulse Assisted Prehospital International Resuscitation (ASPIRE) trial investigators respond to inhomogeneity and temporal effects assertions

To the Editor,

We read with interest the article by Paradis et al [1] offering a reanalysis of the AutoPulse Assisted Prehospital International Resuscitation (ASPIRE) trial originally pub- lished in 2006 [2]. Paradis and colleagues conclude a temporal relationship existed between the AutoPulse and 4- hour survival among a post hoc study population. They report that the outcome of the intervention arm improved during the course of the study among 4 of the 5 sites, which may represent a learning curve in the intervention arm. They separate site C from these analyses because of heterogeneity and conclude that the null or negative association of the AutoPulse intervention was due to a protocol change at site C that limited the AutoPulse use, suggesting that if the AutoPulse had been deployed earlier (and for longer), the result may have been more favorable.

Although post hoc analyses can sometimes provide useful information, the Paradis investigation requires a specific response so that the reader can make an informed assessment of the study’s merit.

The Paradis study uses a different study population and analytic approach than the ASPIRE trial as originally planned. Before trial initiation, the study sponsor, the manufacturer of the AutoPulse, approved the study design including the study population, intervention implementa- tion, primary and secondary outcomes, and the analytic plan. The investigators would not have undertaken the trial if we did not believe that the intervention might improve outcome. The published results, derived from preplanned analyses, were disappointing to the investiga- tors. To dismiss the results of those a priori analyses for post hoc assessment is bad science and, in this case, ethically objectionable given the real potential for harm that was observed.

The Paradis investigation focuses on the 4-hour survival outcome. Although this intermediate clinical measure was the primary outcome, the data and safety monitoring board (DSMB) and the investigators were also charged with monitoring safety-specifically, survival to hospital dis- charge and Neurologically intact survival. The safety assessment is paramount in such a trial given its requisite use of the emergency exception from informed consent. The decision to stop the study early was motivated by the need to assure patient safety.

With regard specifically to the primary study popula- tion, we agree that the etiology of a cardiac arrest may not be discernable at the time of resuscitation from the event. However, there is no reason to believe that the assessment of etiology was biased by the treatment arm. As they point out, Paradis et al made a post hoc decision to include all cardiac arrests regardless of etiology after observing

relationships and outcomes in the noncardiac group. This larger population was not the a priori population, yet we present subsequent results with the combined cardiac and noncardiac groups so that the reader can appreciate that subsequent contrasting findings are not due to different study populations.

With regard to a potential learning curve, the sponsor received a de-identified dataset to comply with privacy requirements. Date of arrest was removed, and the order of patient entry into the study was substituted, which Paradis et al used to assess a learning curve. The order of patient entry into the study is conflated with site because sites came on board during a period of 5 months, and the duration of the trial was only 9 months. Thus, entry order is not a rigorous assessment for evaluating a learning curve. In the original trial publication, we noted that using time from site startup as a measure for assessing a learning curve did not yield a significant association with survival to discharge. The results are presented in Table 1.

The results do not indicate an improvement over time in outcome associated with the AutoPulse intervention, espe- cially with regard to the safety outcome of survival. At most, there may be some suggestion of a waning Hawthorne effect on 4-hour survival in the manual cardiopulmonary resusci- tation (CPR) arm of the other sites.

The authors indicate that a switch in AutoPulse implementation at site C was the reason for the null or negative results. The switch in treatment was from one approved approach to another approved approach. Site C switched from option 1 (evaluation of cardiac rhythm, 2 minutes of randomized AutoPulse or Manual CPR, then Electrical shock if appropriate) to treatment option 2 (2 minutes of manual CPR, shock if appropriate, then randomized AutoPulse or manual CPR) on December 28, 2004. The change in treatment options on December 28 was

Table 1 Randomized study arm, all patients, intent to treat Manual CPR AutoPulse CPR
		Valid n	Proportion	Proportion		Valid n	Proportion	Proportion
			surviving >=4 hours after	discharged alive			surviving >=4 hours after	discharged alive
			911 call				911 call
Other sites Months from initiation	1	81	0.235	0.074		119	0.244	0.050
of study at each site	2	91	0.308	0.077		108	0.287	0.083
	3	53	0.377	0.113		58	0.224	0.086
	4	49	0.224	0.020		51	0.216	0.039
	5	45	0.178	0.089		55	0.273	0.055
	6	60	0.183	0.017		40	0.400	0.075
	7	33	0.182	0.030		27	0.333	0.037
Site C Months from	1	32	0.563	0.406		18	0.500	0.167
initiation of study	2	28	0.464	0.250		22	0.409	0.182
	3	19	0.368	0.158		31	0.387	0.129
	4	25	0.400	0.160		25	0.160	0.000
	5	1	1.000	1.000

Patients	Other	Died	101	328	429
randomized	sites		86.3%	96.2%	93.7%
to the		Discharged	16	13	29
AutoPulse	alive		13.7%	3.8%	6.3%
study arm	Site C	Died	7	78	85
			77.8%	89.7%	88.5%
		Discharged	2	9	11
		alive	22.2%	10.3%	11.5%

initiated by site C leadership after careful assessment had shown that, strictly adhered to, treatment option 1 resulted in a Prolonged pause in chest compressions during a particu- larly vulnerable time.

Table 2 AutoPulse use attempted

No

Yes Total

During the ASPIRE trial, only site C largely complied with option 1. The other sites began manual CPR while getting the AutoPulse ready. Thus, the change on December 28 made site C subsequently more homogenous with the other sites’ approach to AutoPulse application. Indeed site C was more likely to apply the AutoPulse (91% (87/96) versus 74% (341/458; see Table 2). In the AutoPulse arm of the trial, 9 (82%) of 11 survivors at site C had some AutoPulse use, whereas only 13 (45%) of 29 survivors at the other sites had AutoPulse use. If the AutoPulse was used, 96% of the patients died at the other sites compared with 90% mortality at site C.

In this regard, site C was the only site that had basic life support providers can apply using the device. The AutoPulse was applied earliest and used for longer periods by emergency medical services at site C than by the other sites (before or after the protocol change). Consequently, any dose effect assessment would rank site C as delivering the greatest AutoPulse dose.

Paradis and colleagues also hint that the DSMB may not have acted appropriately in recommending early stoppage of the trial. Though there may be some rationale for picking the date December 28, 2004 (when site C switched protocols), there is at least as good a rationale for picking the date February 1, 2005, which is the end date for the data initially reviewed by the DSMB. Enrollment in

the study continued in February and March 2005, while the data through February 1 were compiled and then reviewed by the DSMB. As Table 3 indicates, there is no evidence of a trend over time toward benefit in the AutoPulse arm in the other sites and substantial evidence of harm in site C, and nothing improved after February 1, reaffirming the DSMB’s concern.

Some readers will be challenged by the statistical acrobatics of the Paradis study and so may in turn accept them as an optimal interpretation. A major value of randomized trials is that they enable straightforward, intuitive comparisons and do not rely on advanced statistical methods. The straightforward comparison pre- sented in Table 4-that includes all subjects (cardiac and noncardiac)-indicates no effect on short-term survival and a strong suggestion of harm when evaluating survival to hospital discharge.

How one should test for heterogeneity and how heterogeneity should be addressed in randomized trials are not clearly defined. The “flaw” of heterogeneity could be viewed as a benefit for an intention-to-treat trial that sought to provide real-life experience in varioUS settings and thus generalizable results. There was no a priori reason to think that the intervention effects would be site-specific, so that site is a post hoc subgroup analysis. However, if one decides that site C seems exceptional, Table 5 presents the simple post hoc analysis.

The conclusion seems to be that at one site (historically, the most adept at resuscitation), the AutoPulse adversely affected survival, whereas at the other sites, the AutoPulse did not improve survival. The manual CPR in the ASPIRE trial followed the American Heart Association Guidelines 2000 with a 15:2 compression to ventilation ratio, and thus, prolonged pauses in compressions were likely common, especially at sites A, B, D, and E. One might reasonably expect that survival improved with implemen- tation of 2005 Guidelines CPR [3,4]. Thus, manual CPR might be favored even more strongly today.

The evidence from this rigorous trial is that the AutoPulse has no survival advantage and may be harmful. For now, the AutoPulse should be used only in the context of clinical research until evidence can sufficiently

Table 3 Randomized arm, all patients, intent to treat Manual CPR AutoPulse CPR
	Valid n	Proportion surviving >=4 h p 911	Proportion discharged alive		Valid n	Proportion surviving >=4 h p 911	Proportion discharged alive
Other sites Pre-December 28	192	0.333	0.073		257	0.265	0.062
December 28 to January 31	71	0.155	0.042		85	0.294	0.071
February 1 to March 31	149	0.188	0.060		116	0.267	0.060
Site C Pre-December 28	60	0.517	0.333		44	0.455	0.205
December 28 to January 31	20	0.400	0.150		28	0.393	0.071
February 1 to March 31	25	0.400	0.200		24	0.125	0.000

Table 4 Randomized arm, all patients, intent to treat Manual CPR AutoPulse
	Valid n	Proportion surviving >=4 h p 911	Proportion discharged alive		Valid n	Proportion surviving >=4 h p 911	Proportion discharged alive
All sites	517	0.294	0.104		554	0.285	0.072

Valid n Proportion surviving Proportion discharged					Valid n	Proportion surviving	Proportion discharged
		>=4 h p 911	alive			>=4 h p 911	alive
Other sites	412	0.250	0.063	458		0.271	0.063
Site C	105	0.467	0.267	96		0.354	0.115

explain the ASPIRE results and provide assurance of survival advantage.

Table 5 Randomized arm, all patients, intent to treat

Manual CPR

AutoPulse

Al Hallstrom PhD Thomas D. Rea MD

University of Washington, Seattle WA, USA

Michael R. Sayre MD The Ohio State University, Columbus OH, USA E-mail address: [email protected]

James Christenson MD

University of British Columbia, Vancouver BC, Canada

Leonard Cobb MD

University of Washington, Seattle WA, USA

Vincent N. Mosesso Jr. MD

University of Pittsburgh, Pittsburgh PA, USA

Andy R. Anton MD

Alberta Health Services, Emergency Medical Services

Calgary AB, Canada

doi:10.1016/j.ajem.2010.07.001

References

1. Paradis NA, Young G, Lemeshow S, Brewer JE, Halperin HR. Inhomogeneity and temporal effects in AutoPulse Assisted Prehospital International Resuscitation-an exception from consent trial terminated early. Am J Emerg Med 2010;28(4):391-8.
2. Hallstrom A, Rea TD, Sayre MR, Christenson J, Anton AR, Mosesso Jr VN, et al. Manual chest compression vs use of an automated chest compression device during resuscitation following out-of-hospital cardiac arrest: a randomized trial. JAMA 2006;295(22):2620-8.
3. Rea TD, Helbock M, Perry S, Garcia M, Cloyd D, Becker L, et al. Increasing use of cardiopulmonary resuscitation during out-of-hospital ventricular fibrillation arrest: survival implications of guideline changes. Circulation 2006;114(25):2760-5.
4. Sayre MR, Cantrell SA, White LJ, Hiestand BC, Keseg DP, Koser S. Impact of the 2005 American Heart Association cardiopulmonary resuscitation and Emergency Cardiovascular Care Guidelines on out-of- hospital Cardiac arrest survival. Prehosp Emerg Care 2009;13(4):469-77.

Response to ASPIRE Investigators

To the Editor,

We appreciate the letter and additional data provided by Sayre et al. We believe their response is actually supportive of our concerns: (1) individual ASPIRE trial sites lacked homogeneity before and during the trial [1]; (2) the protocol and execution of the trial allowed individual sites to change the protocol during the trial; (3) the apparent potential harm from the use of the device appears to be isolated to one site after a change in the protocol at that site.

Please allow us to emphasize that we did not “conclude” in our retrospective analysis that a positive temporal relationship existed between the AutoPulse and survival at 4 of the 5 sites, only that our results were hypothesis-generating. Nor do we “dismiss” the results from ASPIRE; we merely offered an alternative hypothesis that we believe may be supported by the data. Although we clearly have significant conflicts with the trial sponsor, we would like to emphasize that our publication was independent of that sponsor.

In a multicenter trial, site data must be homogenous if the data are to be analyzed in aggregate. As Lewis notes in his introduction to the international clinical trial guidelines document [2], “If heterogeneity of treatment effects is found, this should be interpreted with care and vigorous attempts should be made to find an explanation in terms of other features of trial management or subjeCT characteristics. Such an explanation will usually suggest appropriate further analysis and interpretation.”

To detect heterogeneity, we used standard statistical methods, so we do not believe they should be characterized as “acrobatics.” These methods were reviewed by