Andrew D. Auerbach, MD, MPH

Literature Search and Inclusion and Exclusion Criteria

We systematically searched MEDLINE, CINAHL, and BIOSIS through August 2006 for relevant studies using the various terms for RRSs (eg, medical emergency team, rapid response team, critical care outreach) and medical subject headings relevant to inpatient care and critical illness (eg, patient care team and resuscitation; the full search strategy is given in the Appendix). We also reviewed the abstract lists from the 2004 and 2005 American Thoracic Society and Society of Critical Care Medicine annual meetings and scanned reference lists from key articles.

We screened the abstracts of the articles identified by the search, and 2 independent reviewers abstracted potentially relevant articles using a standardized data abstraction form. Disagreements between the reviewers were resolved by consensus and, if necessary, discussion with a third reviewer. We included randomized controlled trials (RCTs), controlled before‐after studies, and interrupted time series, including simple before‐after studies with no contemporaneous control group, though we planned to separately analyze data from controlled studies if possible. We included only English‐language articles.

On the basis of RRS features in widely cited articles2224 and the recommendations of a recent consensus statement,5 we defined an RRS as having the following characteristics: (1) its primary responsibility is to intervene whenever hospitalized patients become unstable before cardiopulmonary arrest occurs; (2) it must primarily provide care outside the ICU and emergency department; (3) specific clinical criteria must be in place that define instability and trigger a call to the team; and (4) it must be expected to respond within a specified time. We defined these criteria in order to distinguish studies of RRSs from studies of cardiac arrest (code blue) teams or traditional consulting services.

To be included in the analysis, articles had to report the effects of a rapid response system on at least 1 of these outcomes: inpatient mortality, inpatient cardiac arrest, or unscheduled ICU transfer. We used the definitions of cardiac arrest and unscheduled ICU transfer given in the primary studies. In addition to these outcomes, we abstracted information on the number of admissions and the number of RRS calls during the study period. To maximize the comparability of study outcomes, we calculated the rates of mortality, cardiac arrest, unscheduled ICU transfer, and RRS calls per 1000 admissions for studies that did not supply data in this fashion.

Assessment of Study Quality

Quality scoring instruments for studies included in systematic reviews generally focus on randomized controlled trials, which we anticipated would account for a minority of included studies. On the basis of recommendations for the assessment of methodology for nonrandomized study designs,25, 26 we identified and abstracted 4 important determinants of internal validity (Table 1). The consensus statement5 recommends monitoring the effectiveness of RRSs by measuring the rate of unscheduled ICU admissions (defined as an unplanned admission to the ICU from a general ward27) and cardiac arrests of patients who were not listed as do not resuscitate (DNR). As the definition of unscheduled ICU admission allows room for subjectivity, we considered the blinding of assessment of this outcome to study group assignment to be important, especially for retrospective studies. Measurement of cardiac arrests should be less susceptible to blinding issues, but one of the functions of an RRS can be to initiate discussions that result in changes in the goals of care and code status.22 Thus, excluding patients made DNR by the team from cardiac arrest calculations could falsely lower the cardiac arrest rate.

We also abstracted 3 separate elements of study quality pertaining to the external validity or generalizability of included studies (Table 1). These elements were defined a priori by consensus reached by discussion among the reviewers. These elements were intended to provide a framework for interpreting the included studies and to guide subgroup analyses. They were not used to form a composite quality score.

Statistical Analysis

We performed a random‐effects meta‐analysis to calculate summary risk ratios with 95% confidence intervals for the effects of RRSs on inpatient mortality, cardiopulmonary arrest, and unscheduled ICU admission. Included in the meta‐analysis were the studies that reported total number of admissions and incidence of each outcome before and after institution of the RRS. For randomized trials that reported pre‐ and postintervention data, we treated the intervention and control groups as separate trials in order to be able to compare their effects with the before‐after trials. For studies that reported results adjusted for clustering (ie, by hospital), we back‐calculated the unadjusted results by multiplying the standard error by the square of the design factor coefficient.28, 29 We calculated the I² statistic to assess heterogeneity.30 All analyses were performed using Stata version 8.2 (Stata Corporation, College Station, TX).

Characteristics of Included Trials

The characteristics of included studies are outlined in Table 2. Five studies were performed in Australia, 4 in the United States, and 4 in the United Kingdom. All were conducted in academic teaching hospitals. Two studies37, 38 focused on pediatric inpatients, and the remainder involved hospitalized adults. The RRS intervened for all hospitalized patients in all but 2 studies (1 of which focused on surgical inpatients33 and the other in which the RRS evaluated only patients discharged from the ICU3). In 2 studies,31, 39 the RRS was available to evaluate outpatients, such as hospital visitors, in addition to inpatients.0

RRS Structure, Calling Criteria, and Responsibilities

Seven studies22, 23, 31, 33, 34, 36, 37 that described the team composition used variants of the medical emergency team model, a physician‐led team (Table 2). In 6 of these 7 studies, the team included a critical care physician (attending or fellow) and an ICU nurse; in the sole RCT (the MERIT study36), the team structure varied between hospitals, consisting of a nurse and physician from either the emergency department or ICU. Hospitalists, who are involved in RRS responses at many U.S. hospitals, were primary team leaders of the RRS in only 1 study.31 In 2 studies34, 37 the RRS also responded to code blue calls, and in 4 studies23, 31, 33, 39 the RRS and the code blue team had separate personnel; the remaining studies did not define the distinction between RRS and code blue team.

In 4 studies the RRSs were led by nurses. One study published in abstract form39 used the rapid response team model, consisting of a critical care nurse and a respiratory therapist, with assistance as needed from the primary medical staff and a critical care physician. Three studies3, 24, 35 from UK hospitals used the critical care outreach (CCO) model, in which ICU‐trained nurses respond initially with assistance from intensivists. The CCO model also involves follow‐up on patients discharged from the ICU and proactive rounding on unstable ward patients.

The hospitals used broadly similar approaches to determining when to summon the RRS, relying on combinations of objective clinical criteria (eg, vital sign abnormalities) and subjective criteria (eg, acute mental status change, staff member concerned about patient's condition). Three studies3, 24, 35 used a formal clinical score (the Patient‐At‐Risk score or the Modified Early Warning score) to trigger calls to the RRS. Three studies, 2 of them from the same institution,23, 33 reported the frequency of specific triggers for RRS activation. Concern by bedside staff and respiratory distress were the most frequent activators of the RRS.

Study Internal Validity and Generalizability

One study,36 the MERIT trial, conducted in Australia, was a cluster‐randomized RCT (randomized by hospital) that adhered to recommended elements of design and reporting for studies of this type.41 In this study, hospitals in the control group received an educational intervention on caring for deteriorating patients only; hospitals in the intervention group received the educational module and started an RRS. An additional study35 identified itself as a randomized trial, but randomization occurred at the hospital ward level, with introduction of the intervention (critical care outreach) staggered so that at different points an individual ward could have been in either the control or intervention group; therefore, this study was considered an interrupted time series. All other trials included were before‐after studies with no contemporaneous control group

Most studies did not meet criteria for internal validity or generalizability (Table 2). Two studies3, 35 did not report the number of RRS calls during the study period. One study22 omitted patients whose resuscitation status was changed after RRS evaluation from the calculation of inpatient mortality; thus, the patients who had been made do not resuscitate by the RRS did not contribute to the calculated mortality rate. The disposition of these patients was unclear in another study.36 All studies measured clinical outcomes retrospectively, and no studies reported blinding of outcomes assessors for nonobjective outcomes (eg, unplanned ICU admission). Studies generally did not report on the availability of intensivists or if other quality improvement interventions targeting critically ill patients were implemented along with the RRS.

RRS Usage and Effects on Patient Outcomes

Seven studies2224, 34, 3638 reported enough information to calculate the RRS calling rate (4 studies24, 31, 39, 40 reported the total number of calls but not the number of admissions, and 2 studies3, 35 did not report either). In these 7 studies, the calling rate varied from 4.5 to 25.8 calls per 1000 admissions. Three studies documented the calling rate before and after the intervention: a study at a hospital with a preexisting RRS34 reported that the calling rate increased from 13.7 to 25.8 calls per 1000 admissions after an intensive education and publicity program; in a pediatric trial,38 the overall emergency calling rate (for cardiac arrests and medical emergencies) was reported to increase from 6.6 to 10.4 per 1000 admissions; and in the MERIT trial,36 calls increased from 3.1 to 8.7 per 1000 admissions.

Effects of RRS on Clinical Outcomes

Nine studies3, 22, 23, 33, 3537, 39, 40 reported the effect of an RRS on inpatient mortality, 9 studies22, 23, 31, 33, 34, 3638, 40 reported its effect on cardiopulmonary arrests, and 6 studies3, 22, 24, 33, 36, 37 reported its effect on unscheduled ICU admissions. Of these, 7 trials that reported mortality and cardiopulmonary arrests and 6 studies that reported unscheduled ICU admissions supplied sufficient data for meta‐analysis.

Observational studies demonstrated improvement in inpatient mortality, with a summary risk ratio of 0.82 (95% CI: 0.74‐0.91, heterogeneity I² 62.1%; Fig. 2). However, the magnitude of these improvements was very similar to that seen in the control group of the MERIT trial (RR 0.73, 95% CI: 0.53‐1.02). The intervention group of the MERIT trial also demonstrated a reduction in mortality that was not significantly different from that of the control group (RR 0.65, 95% CI: 0.48‐0.87). We found a similar pattern in studies reporting RRS effects on cardiopulmonary arrests (Fig. 3). The observational studies did not show any effect on the risk of unscheduled ICU admissions (summary RR 1.08, 95% CI: 0.96‐1.22, heterogeneity I² 79.1%) nor did the MERIT trial (Fig. 4).

Figure 2

Figure 3

Figure 4

Literature Search and Inclusion and Exclusion Criteria

We systematically searched MEDLINE, CINAHL, and BIOSIS through August 2006 for relevant studies using the various terms for RRSs (eg, medical emergency team, rapid response team, critical care outreach) and medical subject headings relevant to inpatient care and critical illness (eg, patient care team and resuscitation; the full search strategy is given in the Appendix). We also reviewed the abstract lists from the 2004 and 2005 American Thoracic Society and Society of Critical Care Medicine annual meetings and scanned reference lists from key articles.

We screened the abstracts of the articles identified by the search, and 2 independent reviewers abstracted potentially relevant articles using a standardized data abstraction form. Disagreements between the reviewers were resolved by consensus and, if necessary, discussion with a third reviewer. We included randomized controlled trials (RCTs), controlled before‐after studies, and interrupted time series, including simple before‐after studies with no contemporaneous control group, though we planned to separately analyze data from controlled studies if possible. We included only English‐language articles.

On the basis of RRS features in widely cited articles2224 and the recommendations of a recent consensus statement,5 we defined an RRS as having the following characteristics: (1) its primary responsibility is to intervene whenever hospitalized patients become unstable before cardiopulmonary arrest occurs; (2) it must primarily provide care outside the ICU and emergency department; (3) specific clinical criteria must be in place that define instability and trigger a call to the team; and (4) it must be expected to respond within a specified time. We defined these criteria in order to distinguish studies of RRSs from studies of cardiac arrest (code blue) teams or traditional consulting services.

To be included in the analysis, articles had to report the effects of a rapid response system on at least 1 of these outcomes: inpatient mortality, inpatient cardiac arrest, or unscheduled ICU transfer. We used the definitions of cardiac arrest and unscheduled ICU transfer given in the primary studies. In addition to these outcomes, we abstracted information on the number of admissions and the number of RRS calls during the study period. To maximize the comparability of study outcomes, we calculated the rates of mortality, cardiac arrest, unscheduled ICU transfer, and RRS calls per 1000 admissions for studies that did not supply data in this fashion.

Assessment of Study Quality

Quality scoring instruments for studies included in systematic reviews generally focus on randomized controlled trials, which we anticipated would account for a minority of included studies. On the basis of recommendations for the assessment of methodology for nonrandomized study designs,25, 26 we identified and abstracted 4 important determinants of internal validity (Table 1). The consensus statement5 recommends monitoring the effectiveness of RRSs by measuring the rate of unscheduled ICU admissions (defined as an unplanned admission to the ICU from a general ward27) and cardiac arrests of patients who were not listed as do not resuscitate (DNR). As the definition of unscheduled ICU admission allows room for subjectivity, we considered the blinding of assessment of this outcome to study group assignment to be important, especially for retrospective studies. Measurement of cardiac arrests should be less susceptible to blinding issues, but one of the functions of an RRS can be to initiate discussions that result in changes in the goals of care and code status.22 Thus, excluding patients made DNR by the team from cardiac arrest calculations could falsely lower the cardiac arrest rate.

We also abstracted 3 separate elements of study quality pertaining to the external validity or generalizability of included studies (Table 1). These elements were defined a priori by consensus reached by discussion among the reviewers. These elements were intended to provide a framework for interpreting the included studies and to guide subgroup analyses. They were not used to form a composite quality score.

Statistical Analysis

We performed a random‐effects meta‐analysis to calculate summary risk ratios with 95% confidence intervals for the effects of RRSs on inpatient mortality, cardiopulmonary arrest, and unscheduled ICU admission. Included in the meta‐analysis were the studies that reported total number of admissions and incidence of each outcome before and after institution of the RRS. For randomized trials that reported pre‐ and postintervention data, we treated the intervention and control groups as separate trials in order to be able to compare their effects with the before‐after trials. For studies that reported results adjusted for clustering (ie, by hospital), we back‐calculated the unadjusted results by multiplying the standard error by the square of the design factor coefficient.28, 29 We calculated the I² statistic to assess heterogeneity.30 All analyses were performed using Stata version 8.2 (Stata Corporation, College Station, TX).

Characteristics of Included Trials

The characteristics of included studies are outlined in Table 2. Five studies were performed in Australia, 4 in the United States, and 4 in the United Kingdom. All were conducted in academic teaching hospitals. Two studies37, 38 focused on pediatric inpatients, and the remainder involved hospitalized adults. The RRS intervened for all hospitalized patients in all but 2 studies (1 of which focused on surgical inpatients33 and the other in which the RRS evaluated only patients discharged from the ICU3). In 2 studies,31, 39 the RRS was available to evaluate outpatients, such as hospital visitors, in addition to inpatients.0

RRS Structure, Calling Criteria, and Responsibilities

Seven studies22, 23, 31, 33, 34, 36, 37 that described the team composition used variants of the medical emergency team model, a physician‐led team (Table 2). In 6 of these 7 studies, the team included a critical care physician (attending or fellow) and an ICU nurse; in the sole RCT (the MERIT study36), the team structure varied between hospitals, consisting of a nurse and physician from either the emergency department or ICU. Hospitalists, who are involved in RRS responses at many U.S. hospitals, were primary team leaders of the RRS in only 1 study.31 In 2 studies34, 37 the RRS also responded to code blue calls, and in 4 studies23, 31, 33, 39 the RRS and the code blue team had separate personnel; the remaining studies did not define the distinction between RRS and code blue team.

In 4 studies the RRSs were led by nurses. One study published in abstract form39 used the rapid response team model, consisting of a critical care nurse and a respiratory therapist, with assistance as needed from the primary medical staff and a critical care physician. Three studies3, 24, 35 from UK hospitals used the critical care outreach (CCO) model, in which ICU‐trained nurses respond initially with assistance from intensivists. The CCO model also involves follow‐up on patients discharged from the ICU and proactive rounding on unstable ward patients.

The hospitals used broadly similar approaches to determining when to summon the RRS, relying on combinations of objective clinical criteria (eg, vital sign abnormalities) and subjective criteria (eg, acute mental status change, staff member concerned about patient's condition). Three studies3, 24, 35 used a formal clinical score (the Patient‐At‐Risk score or the Modified Early Warning score) to trigger calls to the RRS. Three studies, 2 of them from the same institution,23, 33 reported the frequency of specific triggers for RRS activation. Concern by bedside staff and respiratory distress were the most frequent activators of the RRS.

Study Internal Validity and Generalizability

One study,36 the MERIT trial, conducted in Australia, was a cluster‐randomized RCT (randomized by hospital) that adhered to recommended elements of design and reporting for studies of this type.41 In this study, hospitals in the control group received an educational intervention on caring for deteriorating patients only; hospitals in the intervention group received the educational module and started an RRS. An additional study35 identified itself as a randomized trial, but randomization occurred at the hospital ward level, with introduction of the intervention (critical care outreach) staggered so that at different points an individual ward could have been in either the control or intervention group; therefore, this study was considered an interrupted time series. All other trials included were before‐after studies with no contemporaneous control group

Most studies did not meet criteria for internal validity or generalizability (Table 2). Two studies3, 35 did not report the number of RRS calls during the study period. One study22 omitted patients whose resuscitation status was changed after RRS evaluation from the calculation of inpatient mortality; thus, the patients who had been made do not resuscitate by the RRS did not contribute to the calculated mortality rate. The disposition of these patients was unclear in another study.36 All studies measured clinical outcomes retrospectively, and no studies reported blinding of outcomes assessors for nonobjective outcomes (eg, unplanned ICU admission). Studies generally did not report on the availability of intensivists or if other quality improvement interventions targeting critically ill patients were implemented along with the RRS.

RRS Usage and Effects on Patient Outcomes

Seven studies2224, 34, 3638 reported enough information to calculate the RRS calling rate (4 studies24, 31, 39, 40 reported the total number of calls but not the number of admissions, and 2 studies3, 35 did not report either). In these 7 studies, the calling rate varied from 4.5 to 25.8 calls per 1000 admissions. Three studies documented the calling rate before and after the intervention: a study at a hospital with a preexisting RRS34 reported that the calling rate increased from 13.7 to 25.8 calls per 1000 admissions after an intensive education and publicity program; in a pediatric trial,38 the overall emergency calling rate (for cardiac arrests and medical emergencies) was reported to increase from 6.6 to 10.4 per 1000 admissions; and in the MERIT trial,36 calls increased from 3.1 to 8.7 per 1000 admissions.

Effects of RRS on Clinical Outcomes

Nine studies3, 22, 23, 33, 3537, 39, 40 reported the effect of an RRS on inpatient mortality, 9 studies22, 23, 31, 33, 34, 3638, 40 reported its effect on cardiopulmonary arrests, and 6 studies3, 22, 24, 33, 36, 37 reported its effect on unscheduled ICU admissions. Of these, 7 trials that reported mortality and cardiopulmonary arrests and 6 studies that reported unscheduled ICU admissions supplied sufficient data for meta‐analysis.

Observational studies demonstrated improvement in inpatient mortality, with a summary risk ratio of 0.82 (95% CI: 0.74‐0.91, heterogeneity I² 62.1%; Fig. 2). However, the magnitude of these improvements was very similar to that seen in the control group of the MERIT trial (RR 0.73, 95% CI: 0.53‐1.02). The intervention group of the MERIT trial also demonstrated a reduction in mortality that was not significantly different from that of the control group (RR 0.65, 95% CI: 0.48‐0.87). We found a similar pattern in studies reporting RRS effects on cardiopulmonary arrests (Fig. 3). The observational studies did not show any effect on the risk of unscheduled ICU admissions (summary RR 1.08, 95% CI: 0.96‐1.22, heterogeneity I² 79.1%) nor did the MERIT trial (Fig. 4).

Figure 2

Figure 3

Figure 4

Literature Search and Inclusion and Exclusion Criteria

We systematically searched MEDLINE, CINAHL, and BIOSIS through August 2006 for relevant studies using the various terms for RRSs (eg, medical emergency team, rapid response team, critical care outreach) and medical subject headings relevant to inpatient care and critical illness (eg, patient care team and resuscitation; the full search strategy is given in the Appendix). We also reviewed the abstract lists from the 2004 and 2005 American Thoracic Society and Society of Critical Care Medicine annual meetings and scanned reference lists from key articles.

We screened the abstracts of the articles identified by the search, and 2 independent reviewers abstracted potentially relevant articles using a standardized data abstraction form. Disagreements between the reviewers were resolved by consensus and, if necessary, discussion with a third reviewer. We included randomized controlled trials (RCTs), controlled before‐after studies, and interrupted time series, including simple before‐after studies with no contemporaneous control group, though we planned to separately analyze data from controlled studies if possible. We included only English‐language articles.

On the basis of RRS features in widely cited articles2224 and the recommendations of a recent consensus statement,5 we defined an RRS as having the following characteristics: (1) its primary responsibility is to intervene whenever hospitalized patients become unstable before cardiopulmonary arrest occurs; (2) it must primarily provide care outside the ICU and emergency department; (3) specific clinical criteria must be in place that define instability and trigger a call to the team; and (4) it must be expected to respond within a specified time. We defined these criteria in order to distinguish studies of RRSs from studies of cardiac arrest (code blue) teams or traditional consulting services.

To be included in the analysis, articles had to report the effects of a rapid response system on at least 1 of these outcomes: inpatient mortality, inpatient cardiac arrest, or unscheduled ICU transfer. We used the definitions of cardiac arrest and unscheduled ICU transfer given in the primary studies. In addition to these outcomes, we abstracted information on the number of admissions and the number of RRS calls during the study period. To maximize the comparability of study outcomes, we calculated the rates of mortality, cardiac arrest, unscheduled ICU transfer, and RRS calls per 1000 admissions for studies that did not supply data in this fashion.

Assessment of Study Quality

Quality scoring instruments for studies included in systematic reviews generally focus on randomized controlled trials, which we anticipated would account for a minority of included studies. On the basis of recommendations for the assessment of methodology for nonrandomized study designs,25, 26 we identified and abstracted 4 important determinants of internal validity (Table 1). The consensus statement5 recommends monitoring the effectiveness of RRSs by measuring the rate of unscheduled ICU admissions (defined as an unplanned admission to the ICU from a general ward27) and cardiac arrests of patients who were not listed as do not resuscitate (DNR). As the definition of unscheduled ICU admission allows room for subjectivity, we considered the blinding of assessment of this outcome to study group assignment to be important, especially for retrospective studies. Measurement of cardiac arrests should be less susceptible to blinding issues, but one of the functions of an RRS can be to initiate discussions that result in changes in the goals of care and code status.22 Thus, excluding patients made DNR by the team from cardiac arrest calculations could falsely lower the cardiac arrest rate.

We also abstracted 3 separate elements of study quality pertaining to the external validity or generalizability of included studies (Table 1). These elements were defined a priori by consensus reached by discussion among the reviewers. These elements were intended to provide a framework for interpreting the included studies and to guide subgroup analyses. They were not used to form a composite quality score.

Statistical Analysis

We performed a random‐effects meta‐analysis to calculate summary risk ratios with 95% confidence intervals for the effects of RRSs on inpatient mortality, cardiopulmonary arrest, and unscheduled ICU admission. Included in the meta‐analysis were the studies that reported total number of admissions and incidence of each outcome before and after institution of the RRS. For randomized trials that reported pre‐ and postintervention data, we treated the intervention and control groups as separate trials in order to be able to compare their effects with the before‐after trials. For studies that reported results adjusted for clustering (ie, by hospital), we back‐calculated the unadjusted results by multiplying the standard error by the square of the design factor coefficient.28, 29 We calculated the I² statistic to assess heterogeneity.30 All analyses were performed using Stata version 8.2 (Stata Corporation, College Station, TX).

Characteristics of Included Trials

The characteristics of included studies are outlined in Table 2. Five studies were performed in Australia, 4 in the United States, and 4 in the United Kingdom. All were conducted in academic teaching hospitals. Two studies37, 38 focused on pediatric inpatients, and the remainder involved hospitalized adults. The RRS intervened for all hospitalized patients in all but 2 studies (1 of which focused on surgical inpatients33 and the other in which the RRS evaluated only patients discharged from the ICU3). In 2 studies,31, 39 the RRS was available to evaluate outpatients, such as hospital visitors, in addition to inpatients.0

RRS Structure, Calling Criteria, and Responsibilities

Seven studies22, 23, 31, 33, 34, 36, 37 that described the team composition used variants of the medical emergency team model, a physician‐led team (Table 2). In 6 of these 7 studies, the team included a critical care physician (attending or fellow) and an ICU nurse; in the sole RCT (the MERIT study36), the team structure varied between hospitals, consisting of a nurse and physician from either the emergency department or ICU. Hospitalists, who are involved in RRS responses at many U.S. hospitals, were primary team leaders of the RRS in only 1 study.31 In 2 studies34, 37 the RRS also responded to code blue calls, and in 4 studies23, 31, 33, 39 the RRS and the code blue team had separate personnel; the remaining studies did not define the distinction between RRS and code blue team.

In 4 studies the RRSs were led by nurses. One study published in abstract form39 used the rapid response team model, consisting of a critical care nurse and a respiratory therapist, with assistance as needed from the primary medical staff and a critical care physician. Three studies3, 24, 35 from UK hospitals used the critical care outreach (CCO) model, in which ICU‐trained nurses respond initially with assistance from intensivists. The CCO model also involves follow‐up on patients discharged from the ICU and proactive rounding on unstable ward patients.

The hospitals used broadly similar approaches to determining when to summon the RRS, relying on combinations of objective clinical criteria (eg, vital sign abnormalities) and subjective criteria (eg, acute mental status change, staff member concerned about patient's condition). Three studies3, 24, 35 used a formal clinical score (the Patient‐At‐Risk score or the Modified Early Warning score) to trigger calls to the RRS. Three studies, 2 of them from the same institution,23, 33 reported the frequency of specific triggers for RRS activation. Concern by bedside staff and respiratory distress were the most frequent activators of the RRS.

Study Internal Validity and Generalizability

One study,36 the MERIT trial, conducted in Australia, was a cluster‐randomized RCT (randomized by hospital) that adhered to recommended elements of design and reporting for studies of this type.41 In this study, hospitals in the control group received an educational intervention on caring for deteriorating patients only; hospitals in the intervention group received the educational module and started an RRS. An additional study35 identified itself as a randomized trial, but randomization occurred at the hospital ward level, with introduction of the intervention (critical care outreach) staggered so that at different points an individual ward could have been in either the control or intervention group; therefore, this study was considered an interrupted time series. All other trials included were before‐after studies with no contemporaneous control group

Most studies did not meet criteria for internal validity or generalizability (Table 2). Two studies3, 35 did not report the number of RRS calls during the study period. One study22 omitted patients whose resuscitation status was changed after RRS evaluation from the calculation of inpatient mortality; thus, the patients who had been made do not resuscitate by the RRS did not contribute to the calculated mortality rate. The disposition of these patients was unclear in another study.36 All studies measured clinical outcomes retrospectively, and no studies reported blinding of outcomes assessors for nonobjective outcomes (eg, unplanned ICU admission). Studies generally did not report on the availability of intensivists or if other quality improvement interventions targeting critically ill patients were implemented along with the RRS.

RRS Usage and Effects on Patient Outcomes

Seven studies2224, 34, 3638 reported enough information to calculate the RRS calling rate (4 studies24, 31, 39, 40 reported the total number of calls but not the number of admissions, and 2 studies3, 35 did not report either). In these 7 studies, the calling rate varied from 4.5 to 25.8 calls per 1000 admissions. Three studies documented the calling rate before and after the intervention: a study at a hospital with a preexisting RRS34 reported that the calling rate increased from 13.7 to 25.8 calls per 1000 admissions after an intensive education and publicity program; in a pediatric trial,38 the overall emergency calling rate (for cardiac arrests and medical emergencies) was reported to increase from 6.6 to 10.4 per 1000 admissions; and in the MERIT trial,36 calls increased from 3.1 to 8.7 per 1000 admissions.

Effects of RRS on Clinical Outcomes

Nine studies3, 22, 23, 33, 3537, 39, 40 reported the effect of an RRS on inpatient mortality, 9 studies22, 23, 31, 33, 34, 3638, 40 reported its effect on cardiopulmonary arrests, and 6 studies3, 22, 24, 33, 36, 37 reported its effect on unscheduled ICU admissions. Of these, 7 trials that reported mortality and cardiopulmonary arrests and 6 studies that reported unscheduled ICU admissions supplied sufficient data for meta‐analysis.

Observational studies demonstrated improvement in inpatient mortality, with a summary risk ratio of 0.82 (95% CI: 0.74‐0.91, heterogeneity I² 62.1%; Fig. 2). However, the magnitude of these improvements was very similar to that seen in the control group of the MERIT trial (RR 0.73, 95% CI: 0.53‐1.02). The intervention group of the MERIT trial also demonstrated a reduction in mortality that was not significantly different from that of the control group (RR 0.65, 95% CI: 0.48‐0.87). We found a similar pattern in studies reporting RRS effects on cardiopulmonary arrests (Fig. 3). The observational studies did not show any effect on the risk of unscheduled ICU admissions (summary RR 1.08, 95% CI: 0.96‐1.22, heterogeneity I² 79.1%) nor did the MERIT trial (Fig. 4).

Figure 2

Figure 3

Figure 4

Coronary Artery Bypass Grafting

Observational studies have shown that patients with CAD (in the CASS study) treated by coronary artery bypass grafting (CABG) surgery versus had a lower mortality (0.9% vs. 2.4%) and fewer nonfatal myocardial infarctions (0.7% vs. 1.1%) than patients treated with medical therapy who underwent noncardiac surgery months or years later.13 This protective effect of CABG lasted approximately 46 years; however, there was no benefit for low‐risk noncardiac procedures. Furthermore, the risk of perioperative mortality (3%) and morbidity associated with the CABG itself was not taken into account, which would have negated its potential benefit.

Percutaneous Coronary Intervention

Several reports suggested that a previous percutaneous coronary intervention (PCI) was also associated with a lower risk of perioperative mortality and nonfatal myocardial infarction (MI) compared to historical controls. Early studies suggested that noncardiac surgery could be performed as early as 710 days after balloon angioplasty (BA). As bare‐metal stents gradually replaced BA, subsequent reports highlighted the increased risk of noncardiac surgery within 2 weeks14 and then within 46 weeks15 after stenting. This was primarily because of in‐stent thrombosis associated with premature discontinuation of dual antiplatelet therapy or increased major bleeding if this therapy was continued. The current recommendation is to wait at least 46 weeks after inserting a bare‐metal stent and to discontinue clopidogrel aspirin at least 5 days before surgery. A recent review from the Mayo Clinic16 found BA to be reasonably safe if patients require surgery soon after cardiac intervention (after 2 weeks).

More recently drug‐eluting stents (DESs) have become the standard; however, the recommendations for antiplatelet therapy (in the absence of surgery) are for a minimum of 23 months after sirolimus‐coated stents and at least 6 months after stents with paclitaxel. There has been very little in the published literature on patients undergoing noncardiac surgery after drug‐eluting stents. A small retrospective review suggested that patients whose DES had been placed a median of 260 days before surgery had few cardiac events in the perioperative period.17 The recommendations of a French task force did not provide strong guidance, probably because of a lack of evidence.18 The only prospective study of stenting and noncardiac surgery involved continuing antiplatelet therapy (or stopping it less than 3 days before surgery) and using unfractionated heparin or enoxaparin in 103 patients. Despite this therapy, 5 patients died, 12 had myocardial infarctions, 22 had elevation of troponin, but only 4 had major bleeding. Patients with stenting less than 35 days before surgery were at the greatest risk.19 In view of these findings, if noncardiac surgery must be performed within 2 months and the patient is appropriate for PCI, balloon angioplasty or a bare‐metal stent is preferred over DES implantation. If a patient has a DES in place (particularly if it has been fewer than 6 months since implantation) and requires noncardiac surgery, the optimal approach would be to continue at least one if not both antiplatelet agents through surgery; if this is not possible, bridging therapy with intravenous IIB/IIIA receptor blockers has been a suggested approach.10

Revascularization Versus No Revascularization: the CARP Trial

The only randomized controlled study to compare invasive and noninvasive strategies was the Coronary Artery Revascularization Prophylaxis (CARP) trial.20 More than 5800 patients with stable cardiac symptoms scheduled for elective nonvascular surgery in VA hospitals were screened, approximately 20% underwent coronary angiography, and 510 patients (9% of the original group) were randomized to PCI/CABG or no revascularization. Revascularization was associated with 1.7% mortality and a 5.8% nonfatal MI rate, and an additional 4% died after successful revascularization while awaiting vascular surgery. Short‐term outcomes were similar in both the revascularization and no revascularization groups (3% 30‐day mortality and 8%12% perioperative nonfatal MI). The primary outcome, long‐term mortality, also did not differ between the groups (22% vs. 23%) after an average follow‐up of 2.7 years. The investigators concluded on the basis of this data that prophylactic revascularization could not be recommended for patients with stable CAD undergoing elective vascular surgery. Of note is that both groups of patients in the CARP trial were given intensive medical therapy, with 84% on beta‐blockers, 54% on statins, 51% on ACE inhibitors, and 73% on aspirin, which may have made it difficult to show any significant benefit of revascularization. Other limitations of that study are that it was underpowered to detect a short‐term benefit and excluded patients with unstable or more severe cardiac symptoms or disease (left main disease, aortic stenosis, and severe left ventricular dysfunction). In any case, the results of this support the ACC guidelines, which state that prophylactic revascularization is rarely necessary just to get the patient through surgery.

If the goal of risk stratification is to determine which patients are at increased risk and if revascularization fails to lower that risk, various medical therapies, including beta‐blockers, alpha‐agonists, and statins, should be considered as risk‐reduction strategies.

Cardioprotection with Adrenergic Modulation and Statin Therapy

Support for adrenergic modulation (with beta‐blockers and alpha‐agonists) to prevent postoperative cardiac complications has been the subject of a number of reviews, including our own.7, 8, 21 Initial enthusiasm22, 23 has been tempered, however, as evidence has evolved.

The results of a randomized trial published in abstract form24 showed no significant difference in rates of a combined end point of mortality, myocardial infarction, heart failure, and ventricular arrhythmia 30 days after vascular surgery of 500 patients randomized to metoprolol or placebo. Furthermore, in a randomized trial of 107 aortic surgery patients with no history of coronary disease, metoprolol started on admission and continued for 7 days did not significantly reduce cardiac events.25 In addition, a well‐designed meta‐analysis suggested that there are too few data to definitively determine whether perioperative beta‐blockade is efficacious.26 Finally, the results of a rigorously analyzed observational trial using administrative data from nearly 700,000 patients suggested that perioperative beta‐blockade was protective (reduced mortality) only in higher‐risk patients (eg, RCRI 2 points). In those at lower risk, beta blockade was associated with a higher risk of complications, even if the lower‐risk patients had only 1 risk factor of either diabetes or coronary disease.27

Trials of alpha adrenergic agonists have also been summarized in at least 2 meta‐analyses. One of these meta‐analyses reported alpha‐2 agonists reduced mortality by nearly half and reduced postoperative myocardial infarction by a third in vascular patients, but had no benefit in others.28 Another meta‐analysis calculated that 83 patients needed to be treated with alpha‐agonists to prevent one cardiac event,29 a number higher than that for beta‐blockers.

Data on the effectiveness of statins is accumulating. The results of 5 observational trials3034 and 1 randomized study35 suggest that patients receiving statin therapy at the time of surgery (and afterward) have a lower risk of having a cardiac event and lower mortality, with relative reductions in risk between 80%30 and 30%.32 In the 1 randomized trial, of 100 vascular surgery patients, 20 mg/day of atorvastatin was begun 1 month before surgery and continued for 45 days,35 with beta‐blockers included per protocol. This protocol reduced the combined outcome of cardiac mortality, myocardial infarction, stroke, or unstable angina, but the overall number of events was very small (4 patients vs. 13 patients, P = .03). However, no patient required discontinuation of the drug because of side effects.

Target Patients Most Likely to Benefit

Recent trends in evidence increasingly support the idea that lower‐risk subgroups (such as those with the minor criteria employed by Mangano) may not benefit from perioperative beta‐blockers and that only higher‐risk subgroups should be targeted. This general approach was recommended in recent guidelines from the AHA‐ACC,36 as well as in an extensive review of perioperative cardiac risk management.10 The strongest recommendations were to continue beta‐blockers in patients already on them and to give them to patients scheduled for vascular surgery who had ischemia on a stress test. The ACC also stated that beta‐blockers were probably recommended for patients with known CAD or high cardiac risk scheduled for intermediate‐ to high‐risk surgery. Recommendations for other groups were weaker or lacked sufficient evidence.36 At this point, it seems prudent to target high‐risk patients (RCRI 2), as well as those who would require beta‐blockers or statin therapy regardless (eg, patients with known coronary artery disease). There are no data to suggest that dose titration of statins is required before surgery.

Be Aware of How Harm Might Be Produced

Notwithstanding its limitations, results from the recent observational trial from Lindenauer raise important questions about the effectiveness of beta‐blockers in practice. That is, are beta‐blockers safe and effective when used in surgical patients outside the tightly controlled setting of a randomized trial? It is apparent how titrating beta‐blockers to a target heart rate without careful clinical assessment (as occurred in most RCTs) might lead to beta‐blockers being used to treat tachycardia related to hypovolemia, pain, anemia, bleeding, or early sepsis. Interestingly, beta‐blockers may be associated with higher risk in other settings as well,37 so potential harm in the perioperative period are not completely surprising.

Use a Protocol That Sticks as Close to the Evidence as Possible

To stay as close as possible to what the evidence shows for the use of beta‐blockers, this drug should be started early enough to allow dose titration and continued for at least 7 days and optimally 30 days after surgery (indefinitely, if a patient requires it long term), working to ensure that patients are physiologically beta‐blocked (eg, heart rate 5565) for as much of the time that they are being treated as possible. Two recent studies demonstrated the importance of tight heart rate control38, 39higher doses of beta‐blockers and tight heart rate control were associated with reduced perioperative myocardial ischemia and troponin T release, which might obviate the need for preoperative cardiac testing in intermediate‐risk patients undergoing vascular surgery. A recent placebo‐controlled, randomized trial40 suggested that a simple strategy of 4 days of transdermal and oral clonidine reduced perioperative ischemia and mortality. Although this approach is very useful for patients who cannot take pills by mouth, it would necessitate a switch to beta‐blockers for patients who need them long term. In addition, use of clonidine may be associated with a higher risk of withdrawal than cardioselective beta‐blockers. No prospective trials have compared beta‐blockers and alpha‐2 agonists. Both produce hypotension and bradycardia, improve pain control, and rarely produce adverse pulmonary effects.41 At the least, consultants should be clear in their recommendations about the start and stop dates for beta‐blockers and should ensure a smooth outpatient transition of patients for whom long‐term statin or beta‐blocker therapy is needed.

Be Ready to Adjust Your Practice as the Evidence Continues to Evolve

Far too few patients have been randomized to beta‐blockers, adrenergic modulation, or statin therapy to date to provide a reasonable estimate of their effects on mortality. As a result, although it seems likely that some subgroups benefit from one or more of these therapies, the degree of risk requiredand an optimal dosing scheduleremains a subject of intense debate. The results of perioperative trials of adrenergic modulators have consistently provided evidence supporting their use in other patient populations, but larger studies may not confirm a beneficial effect. Ongoing Canadian (POISE) and European trials (DECREASE IV) should address sample size limitations and provide information critical for clinicians caring for patients in this era of rapidly evolving evidence.

Coronary Artery Bypass Grafting

Observational studies have shown that patients with CAD (in the CASS study) treated by coronary artery bypass grafting (CABG) surgery versus had a lower mortality (0.9% vs. 2.4%) and fewer nonfatal myocardial infarctions (0.7% vs. 1.1%) than patients treated with medical therapy who underwent noncardiac surgery months or years later.13 This protective effect of CABG lasted approximately 46 years; however, there was no benefit for low‐risk noncardiac procedures. Furthermore, the risk of perioperative mortality (3%) and morbidity associated with the CABG itself was not taken into account, which would have negated its potential benefit.

Percutaneous Coronary Intervention

Several reports suggested that a previous percutaneous coronary intervention (PCI) was also associated with a lower risk of perioperative mortality and nonfatal myocardial infarction (MI) compared to historical controls. Early studies suggested that noncardiac surgery could be performed as early as 710 days after balloon angioplasty (BA). As bare‐metal stents gradually replaced BA, subsequent reports highlighted the increased risk of noncardiac surgery within 2 weeks14 and then within 46 weeks15 after stenting. This was primarily because of in‐stent thrombosis associated with premature discontinuation of dual antiplatelet therapy or increased major bleeding if this therapy was continued. The current recommendation is to wait at least 46 weeks after inserting a bare‐metal stent and to discontinue clopidogrel aspirin at least 5 days before surgery. A recent review from the Mayo Clinic16 found BA to be reasonably safe if patients require surgery soon after cardiac intervention (after 2 weeks).

More recently drug‐eluting stents (DESs) have become the standard; however, the recommendations for antiplatelet therapy (in the absence of surgery) are for a minimum of 23 months after sirolimus‐coated stents and at least 6 months after stents with paclitaxel. There has been very little in the published literature on patients undergoing noncardiac surgery after drug‐eluting stents. A small retrospective review suggested that patients whose DES had been placed a median of 260 days before surgery had few cardiac events in the perioperative period.17 The recommendations of a French task force did not provide strong guidance, probably because of a lack of evidence.18 The only prospective study of stenting and noncardiac surgery involved continuing antiplatelet therapy (or stopping it less than 3 days before surgery) and using unfractionated heparin or enoxaparin in 103 patients. Despite this therapy, 5 patients died, 12 had myocardial infarctions, 22 had elevation of troponin, but only 4 had major bleeding. Patients with stenting less than 35 days before surgery were at the greatest risk.19 In view of these findings, if noncardiac surgery must be performed within 2 months and the patient is appropriate for PCI, balloon angioplasty or a bare‐metal stent is preferred over DES implantation. If a patient has a DES in place (particularly if it has been fewer than 6 months since implantation) and requires noncardiac surgery, the optimal approach would be to continue at least one if not both antiplatelet agents through surgery; if this is not possible, bridging therapy with intravenous IIB/IIIA receptor blockers has been a suggested approach.10

Revascularization Versus No Revascularization: the CARP Trial

The only randomized controlled study to compare invasive and noninvasive strategies was the Coronary Artery Revascularization Prophylaxis (CARP) trial.20 More than 5800 patients with stable cardiac symptoms scheduled for elective nonvascular surgery in VA hospitals were screened, approximately 20% underwent coronary angiography, and 510 patients (9% of the original group) were randomized to PCI/CABG or no revascularization. Revascularization was associated with 1.7% mortality and a 5.8% nonfatal MI rate, and an additional 4% died after successful revascularization while awaiting vascular surgery. Short‐term outcomes were similar in both the revascularization and no revascularization groups (3% 30‐day mortality and 8%12% perioperative nonfatal MI). The primary outcome, long‐term mortality, also did not differ between the groups (22% vs. 23%) after an average follow‐up of 2.7 years. The investigators concluded on the basis of this data that prophylactic revascularization could not be recommended for patients with stable CAD undergoing elective vascular surgery. Of note is that both groups of patients in the CARP trial were given intensive medical therapy, with 84% on beta‐blockers, 54% on statins, 51% on ACE inhibitors, and 73% on aspirin, which may have made it difficult to show any significant benefit of revascularization. Other limitations of that study are that it was underpowered to detect a short‐term benefit and excluded patients with unstable or more severe cardiac symptoms or disease (left main disease, aortic stenosis, and severe left ventricular dysfunction). In any case, the results of this support the ACC guidelines, which state that prophylactic revascularization is rarely necessary just to get the patient through surgery.

If the goal of risk stratification is to determine which patients are at increased risk and if revascularization fails to lower that risk, various medical therapies, including beta‐blockers, alpha‐agonists, and statins, should be considered as risk‐reduction strategies.

Cardioprotection with Adrenergic Modulation and Statin Therapy

Support for adrenergic modulation (with beta‐blockers and alpha‐agonists) to prevent postoperative cardiac complications has been the subject of a number of reviews, including our own.7, 8, 21 Initial enthusiasm22, 23 has been tempered, however, as evidence has evolved.

The results of a randomized trial published in abstract form24 showed no significant difference in rates of a combined end point of mortality, myocardial infarction, heart failure, and ventricular arrhythmia 30 days after vascular surgery of 500 patients randomized to metoprolol or placebo. Furthermore, in a randomized trial of 107 aortic surgery patients with no history of coronary disease, metoprolol started on admission and continued for 7 days did not significantly reduce cardiac events.25 In addition, a well‐designed meta‐analysis suggested that there are too few data to definitively determine whether perioperative beta‐blockade is efficacious.26 Finally, the results of a rigorously analyzed observational trial using administrative data from nearly 700,000 patients suggested that perioperative beta‐blockade was protective (reduced mortality) only in higher‐risk patients (eg, RCRI 2 points). In those at lower risk, beta blockade was associated with a higher risk of complications, even if the lower‐risk patients had only 1 risk factor of either diabetes or coronary disease.27

Trials of alpha adrenergic agonists have also been summarized in at least 2 meta‐analyses. One of these meta‐analyses reported alpha‐2 agonists reduced mortality by nearly half and reduced postoperative myocardial infarction by a third in vascular patients, but had no benefit in others.28 Another meta‐analysis calculated that 83 patients needed to be treated with alpha‐agonists to prevent one cardiac event,29 a number higher than that for beta‐blockers.

Data on the effectiveness of statins is accumulating. The results of 5 observational trials3034 and 1 randomized study35 suggest that patients receiving statin therapy at the time of surgery (and afterward) have a lower risk of having a cardiac event and lower mortality, with relative reductions in risk between 80%30 and 30%.32 In the 1 randomized trial, of 100 vascular surgery patients, 20 mg/day of atorvastatin was begun 1 month before surgery and continued for 45 days,35 with beta‐blockers included per protocol. This protocol reduced the combined outcome of cardiac mortality, myocardial infarction, stroke, or unstable angina, but the overall number of events was very small (4 patients vs. 13 patients, P = .03). However, no patient required discontinuation of the drug because of side effects.

Target Patients Most Likely to Benefit

Recent trends in evidence increasingly support the idea that lower‐risk subgroups (such as those with the minor criteria employed by Mangano) may not benefit from perioperative beta‐blockers and that only higher‐risk subgroups should be targeted. This general approach was recommended in recent guidelines from the AHA‐ACC,36 as well as in an extensive review of perioperative cardiac risk management.10 The strongest recommendations were to continue beta‐blockers in patients already on them and to give them to patients scheduled for vascular surgery who had ischemia on a stress test. The ACC also stated that beta‐blockers were probably recommended for patients with known CAD or high cardiac risk scheduled for intermediate‐ to high‐risk surgery. Recommendations for other groups were weaker or lacked sufficient evidence.36 At this point, it seems prudent to target high‐risk patients (RCRI 2), as well as those who would require beta‐blockers or statin therapy regardless (eg, patients with known coronary artery disease). There are no data to suggest that dose titration of statins is required before surgery.

Be Aware of How Harm Might Be Produced

Notwithstanding its limitations, results from the recent observational trial from Lindenauer raise important questions about the effectiveness of beta‐blockers in practice. That is, are beta‐blockers safe and effective when used in surgical patients outside the tightly controlled setting of a randomized trial? It is apparent how titrating beta‐blockers to a target heart rate without careful clinical assessment (as occurred in most RCTs) might lead to beta‐blockers being used to treat tachycardia related to hypovolemia, pain, anemia, bleeding, or early sepsis. Interestingly, beta‐blockers may be associated with higher risk in other settings as well,37 so potential harm in the perioperative period are not completely surprising.

Use a Protocol That Sticks as Close to the Evidence as Possible

To stay as close as possible to what the evidence shows for the use of beta‐blockers, this drug should be started early enough to allow dose titration and continued for at least 7 days and optimally 30 days after surgery (indefinitely, if a patient requires it long term), working to ensure that patients are physiologically beta‐blocked (eg, heart rate 5565) for as much of the time that they are being treated as possible. Two recent studies demonstrated the importance of tight heart rate control38, 39higher doses of beta‐blockers and tight heart rate control were associated with reduced perioperative myocardial ischemia and troponin T release, which might obviate the need for preoperative cardiac testing in intermediate‐risk patients undergoing vascular surgery. A recent placebo‐controlled, randomized trial40 suggested that a simple strategy of 4 days of transdermal and oral clonidine reduced perioperative ischemia and mortality. Although this approach is very useful for patients who cannot take pills by mouth, it would necessitate a switch to beta‐blockers for patients who need them long term. In addition, use of clonidine may be associated with a higher risk of withdrawal than cardioselective beta‐blockers. No prospective trials have compared beta‐blockers and alpha‐2 agonists. Both produce hypotension and bradycardia, improve pain control, and rarely produce adverse pulmonary effects.41 At the least, consultants should be clear in their recommendations about the start and stop dates for beta‐blockers and should ensure a smooth outpatient transition of patients for whom long‐term statin or beta‐blocker therapy is needed.

Be Ready to Adjust Your Practice as the Evidence Continues to Evolve

Far too few patients have been randomized to beta‐blockers, adrenergic modulation, or statin therapy to date to provide a reasonable estimate of their effects on mortality. As a result, although it seems likely that some subgroups benefit from one or more of these therapies, the degree of risk requiredand an optimal dosing scheduleremains a subject of intense debate. The results of perioperative trials of adrenergic modulators have consistently provided evidence supporting their use in other patient populations, but larger studies may not confirm a beneficial effect. Ongoing Canadian (POISE) and European trials (DECREASE IV) should address sample size limitations and provide information critical for clinicians caring for patients in this era of rapidly evolving evidence.

Coronary Artery Bypass Grafting

Observational studies have shown that patients with CAD (in the CASS study) treated by coronary artery bypass grafting (CABG) surgery versus had a lower mortality (0.9% vs. 2.4%) and fewer nonfatal myocardial infarctions (0.7% vs. 1.1%) than patients treated with medical therapy who underwent noncardiac surgery months or years later.13 This protective effect of CABG lasted approximately 46 years; however, there was no benefit for low‐risk noncardiac procedures. Furthermore, the risk of perioperative mortality (3%) and morbidity associated with the CABG itself was not taken into account, which would have negated its potential benefit.

Percutaneous Coronary Intervention

Several reports suggested that a previous percutaneous coronary intervention (PCI) was also associated with a lower risk of perioperative mortality and nonfatal myocardial infarction (MI) compared to historical controls. Early studies suggested that noncardiac surgery could be performed as early as 710 days after balloon angioplasty (BA). As bare‐metal stents gradually replaced BA, subsequent reports highlighted the increased risk of noncardiac surgery within 2 weeks14 and then within 46 weeks15 after stenting. This was primarily because of in‐stent thrombosis associated with premature discontinuation of dual antiplatelet therapy or increased major bleeding if this therapy was continued. The current recommendation is to wait at least 46 weeks after inserting a bare‐metal stent and to discontinue clopidogrel aspirin at least 5 days before surgery. A recent review from the Mayo Clinic16 found BA to be reasonably safe if patients require surgery soon after cardiac intervention (after 2 weeks).

More recently drug‐eluting stents (DESs) have become the standard; however, the recommendations for antiplatelet therapy (in the absence of surgery) are for a minimum of 23 months after sirolimus‐coated stents and at least 6 months after stents with paclitaxel. There has been very little in the published literature on patients undergoing noncardiac surgery after drug‐eluting stents. A small retrospective review suggested that patients whose DES had been placed a median of 260 days before surgery had few cardiac events in the perioperative period.17 The recommendations of a French task force did not provide strong guidance, probably because of a lack of evidence.18 The only prospective study of stenting and noncardiac surgery involved continuing antiplatelet therapy (or stopping it less than 3 days before surgery) and using unfractionated heparin or enoxaparin in 103 patients. Despite this therapy, 5 patients died, 12 had myocardial infarctions, 22 had elevation of troponin, but only 4 had major bleeding. Patients with stenting less than 35 days before surgery were at the greatest risk.19 In view of these findings, if noncardiac surgery must be performed within 2 months and the patient is appropriate for PCI, balloon angioplasty or a bare‐metal stent is preferred over DES implantation. If a patient has a DES in place (particularly if it has been fewer than 6 months since implantation) and requires noncardiac surgery, the optimal approach would be to continue at least one if not both antiplatelet agents through surgery; if this is not possible, bridging therapy with intravenous IIB/IIIA receptor blockers has been a suggested approach.10

Revascularization Versus No Revascularization: the CARP Trial

The only randomized controlled study to compare invasive and noninvasive strategies was the Coronary Artery Revascularization Prophylaxis (CARP) trial.20 More than 5800 patients with stable cardiac symptoms scheduled for elective nonvascular surgery in VA hospitals were screened, approximately 20% underwent coronary angiography, and 510 patients (9% of the original group) were randomized to PCI/CABG or no revascularization. Revascularization was associated with 1.7% mortality and a 5.8% nonfatal MI rate, and an additional 4% died after successful revascularization while awaiting vascular surgery. Short‐term outcomes were similar in both the revascularization and no revascularization groups (3% 30‐day mortality and 8%12% perioperative nonfatal MI). The primary outcome, long‐term mortality, also did not differ between the groups (22% vs. 23%) after an average follow‐up of 2.7 years. The investigators concluded on the basis of this data that prophylactic revascularization could not be recommended for patients with stable CAD undergoing elective vascular surgery. Of note is that both groups of patients in the CARP trial were given intensive medical therapy, with 84% on beta‐blockers, 54% on statins, 51% on ACE inhibitors, and 73% on aspirin, which may have made it difficult to show any significant benefit of revascularization. Other limitations of that study are that it was underpowered to detect a short‐term benefit and excluded patients with unstable or more severe cardiac symptoms or disease (left main disease, aortic stenosis, and severe left ventricular dysfunction). In any case, the results of this support the ACC guidelines, which state that prophylactic revascularization is rarely necessary just to get the patient through surgery.

If the goal of risk stratification is to determine which patients are at increased risk and if revascularization fails to lower that risk, various medical therapies, including beta‐blockers, alpha‐agonists, and statins, should be considered as risk‐reduction strategies.

Cardioprotection with Adrenergic Modulation and Statin Therapy

Support for adrenergic modulation (with beta‐blockers and alpha‐agonists) to prevent postoperative cardiac complications has been the subject of a number of reviews, including our own.7, 8, 21 Initial enthusiasm22, 23 has been tempered, however, as evidence has evolved.

The results of a randomized trial published in abstract form24 showed no significant difference in rates of a combined end point of mortality, myocardial infarction, heart failure, and ventricular arrhythmia 30 days after vascular surgery of 500 patients randomized to metoprolol or placebo. Furthermore, in a randomized trial of 107 aortic surgery patients with no history of coronary disease, metoprolol started on admission and continued for 7 days did not significantly reduce cardiac events.25 In addition, a well‐designed meta‐analysis suggested that there are too few data to definitively determine whether perioperative beta‐blockade is efficacious.26 Finally, the results of a rigorously analyzed observational trial using administrative data from nearly 700,000 patients suggested that perioperative beta‐blockade was protective (reduced mortality) only in higher‐risk patients (eg, RCRI 2 points). In those at lower risk, beta blockade was associated with a higher risk of complications, even if the lower‐risk patients had only 1 risk factor of either diabetes or coronary disease.27

Trials of alpha adrenergic agonists have also been summarized in at least 2 meta‐analyses. One of these meta‐analyses reported alpha‐2 agonists reduced mortality by nearly half and reduced postoperative myocardial infarction by a third in vascular patients, but had no benefit in others.28 Another meta‐analysis calculated that 83 patients needed to be treated with alpha‐agonists to prevent one cardiac event,29 a number higher than that for beta‐blockers.

Data on the effectiveness of statins is accumulating. The results of 5 observational trials3034 and 1 randomized study35 suggest that patients receiving statin therapy at the time of surgery (and afterward) have a lower risk of having a cardiac event and lower mortality, with relative reductions in risk between 80%30 and 30%.32 In the 1 randomized trial, of 100 vascular surgery patients, 20 mg/day of atorvastatin was begun 1 month before surgery and continued for 45 days,35 with beta‐blockers included per protocol. This protocol reduced the combined outcome of cardiac mortality, myocardial infarction, stroke, or unstable angina, but the overall number of events was very small (4 patients vs. 13 patients, P = .03). However, no patient required discontinuation of the drug because of side effects.

Target Patients Most Likely to Benefit

Recent trends in evidence increasingly support the idea that lower‐risk subgroups (such as those with the minor criteria employed by Mangano) may not benefit from perioperative beta‐blockers and that only higher‐risk subgroups should be targeted. This general approach was recommended in recent guidelines from the AHA‐ACC,36 as well as in an extensive review of perioperative cardiac risk management.10 The strongest recommendations were to continue beta‐blockers in patients already on them and to give them to patients scheduled for vascular surgery who had ischemia on a stress test. The ACC also stated that beta‐blockers were probably recommended for patients with known CAD or high cardiac risk scheduled for intermediate‐ to high‐risk surgery. Recommendations for other groups were weaker or lacked sufficient evidence.36 At this point, it seems prudent to target high‐risk patients (RCRI 2), as well as those who would require beta‐blockers or statin therapy regardless (eg, patients with known coronary artery disease). There are no data to suggest that dose titration of statins is required before surgery.

Be Aware of How Harm Might Be Produced

Notwithstanding its limitations, results from the recent observational trial from Lindenauer raise important questions about the effectiveness of beta‐blockers in practice. That is, are beta‐blockers safe and effective when used in surgical patients outside the tightly controlled setting of a randomized trial? It is apparent how titrating beta‐blockers to a target heart rate without careful clinical assessment (as occurred in most RCTs) might lead to beta‐blockers being used to treat tachycardia related to hypovolemia, pain, anemia, bleeding, or early sepsis. Interestingly, beta‐blockers may be associated with higher risk in other settings as well,37 so potential harm in the perioperative period are not completely surprising.

Use a Protocol That Sticks as Close to the Evidence as Possible

To stay as close as possible to what the evidence shows for the use of beta‐blockers, this drug should be started early enough to allow dose titration and continued for at least 7 days and optimally 30 days after surgery (indefinitely, if a patient requires it long term), working to ensure that patients are physiologically beta‐blocked (eg, heart rate 5565) for as much of the time that they are being treated as possible. Two recent studies demonstrated the importance of tight heart rate control38, 39higher doses of beta‐blockers and tight heart rate control were associated with reduced perioperative myocardial ischemia and troponin T release, which might obviate the need for preoperative cardiac testing in intermediate‐risk patients undergoing vascular surgery. A recent placebo‐controlled, randomized trial40 suggested that a simple strategy of 4 days of transdermal and oral clonidine reduced perioperative ischemia and mortality. Although this approach is very useful for patients who cannot take pills by mouth, it would necessitate a switch to beta‐blockers for patients who need them long term. In addition, use of clonidine may be associated with a higher risk of withdrawal than cardioselective beta‐blockers. No prospective trials have compared beta‐blockers and alpha‐2 agonists. Both produce hypotension and bradycardia, improve pain control, and rarely produce adverse pulmonary effects.41 At the least, consultants should be clear in their recommendations about the start and stop dates for beta‐blockers and should ensure a smooth outpatient transition of patients for whom long‐term statin or beta‐blocker therapy is needed.

Be Ready to Adjust Your Practice as the Evidence Continues to Evolve

Far too few patients have been randomized to beta‐blockers, adrenergic modulation, or statin therapy to date to provide a reasonable estimate of their effects on mortality. As a result, although it seems likely that some subgroups benefit from one or more of these therapies, the degree of risk requiredand an optimal dosing scheduleremains a subject of intense debate. The results of perioperative trials of adrenergic modulators have consistently provided evidence supporting their use in other patient populations, but larger studies may not confirm a beneficial effect. Ongoing Canadian (POISE) and European trials (DECREASE IV) should address sample size limitations and provide information critical for clinicians caring for patients in this era of rapidly evolving evidence.

Sites and Subjects

Details of the sites, subjects, and methods used to collect patient‐level data in this analysis have been previously published.1 The study was performed at Moffitt‐Long Hospital and San Francisco General Hospital, teaching hospitals affiliated with the University of California San Francisco School of Medicine. At both sites, single‐detector CT scans were available 24 hours a day throughout the study period and were read by attending radiologists who specialized in thoracic imaging. We excluded patients whose CTPA was not completed as the initial test in the evaluation of suspected PE, those who underwent testing for any indication other than suspected acute PE, and those with incomplete medical records or technically inadequate CTPA.

We randomly selected 345 patients who underwent CTPA between January 1, 1998, and December 31, 2000, from the Radiology Department databases. One investigator (R.L.T.) then abstracted charts of all patients. For each subject, we collected data about history and clinical presentation, diagnostic impressions of the treating clinicians, treatments administered both before and after diagnostic testing, CTPA result, results of other diagnostic tests for PE, and final clinical diagnosis. During the study period, there were no institution‐ or department‐specific guidelines or decision aids available for the diagnosis of PE. Ventilation‐perfusion scan, lower extremity ultrasound, and pulmonary angiography were available, but highly sensitive D‐dimer assays were not in use. The study was approved by the Institutional Review Boards of both sites, and requirement for written informed consent from patients was waived.

Estimates of Pretest Probabilities of Pulmonary Embolism and CTPA Test Characteristics

Several prediction rules1820 generate clinical pretest probabilities for patients with suspected PE. We used the Wells score18 to assign a pretest probability of low, moderate, or high to each patient on the basis of the following clinical variables: leg swelling, hemoptysis, tachycardia, history of recent immobilization, history of prior DVT or PE, active malignancy, and lack of a more likely alternative diagnosis. We chose this rule as (unlike other prediction rules such as the Geneva rule20) the Wells score has been validated for hospitalized patients with suspected PE and does not require arterial blood gas measurements. The prevalence of PE reported in the evaluation of the Wells score was 3.4%, 27.8%, and 78.3% for low, moderate, and high pretest probabilities, respectively.18

As in our previous study,1 we assumed CTPA to be 90% sensitive and 95% specific based on published estimates.3, 17 These values correspond to a positive likelihood ratio of 18 and a negative likelihood ratio of 0.1.21 We chose these values as a best‐case estimate of the test characteristics of CTPA, although other studies have found less impressive results.7 Using these pretest probabilities and likelihood ratios, we then used Bayes' theorem (Figure 1) to calculate the range of expected posttest probabilities of pulmonary embolism.

Figure 1

Calculation of Posttest Probabilities and Comparison to Treatment Outcomes

For each pretest probability category, we used the posttest probabilities calculated above to determine the number of true‐positive pulmonary emboli, as follows: We then compared treatment decisions made by clinicians at our hospital to the calculated posttest probabilities and number of true‐positive diagnoses of PE. We considered the difference between the number of patients treated for PE and the number of true‐positive diagnoses of PE to represent possible false‐positive diagnoses. In a similar fashion, we determined the number of likely true‐negative diagnoses of PE and considered the difference between the number of patients not treated for PE and the number of true‐negative diagnoses to represent possible false‐negative diagnoses.

Patient Characteristics

After excluding 23 patients receiving anticoagulants for other indications prior to CTPA, the study cohort included 322 patients (57.7% female), with an average age of 58.6 years, of whom 20.5% had cancer and 4.5% had a prior history of thromboembolic disease. Scans were primarily ordered by the medicine service (47.7% of cases) and emergency department (22.9%). CTPA was the initial test for 9% of patients evaluated for suspected acute PE during the first 6 months of the study period, increasing to 83% by the end of 2000.1 The overall pretest probability distribution remained the same throughout the entire study period.1

Test Results and Treatment Decisions

Most patients in our cohort had a low (n = 184, 57.1%) or a moderate (n = 101, 31.4%) pretest probability of PE (Table 1). The likelihood of a positive CTPA increased as the pretest probability increased, but even among patients with high clinical risk, only 35.1% had positive CT scans. In total, scans were positive in 57 patients and negative in 265 patients. Clinicians treated 55 patients with a positive CTPA (96.5%); none of these patients underwent additional testing for DVT or PE after the imaging study. Among patients with a negative CTPA, 254 (95.8%) were not treated; none of the patients in whom anticoagulation was withheld underwent further testing, whereas the other 11 patients were treated on the basis of other tests (5 high‐probability ventilation‐perfusion scans, 3 positive leg ultrasounds, and 3 for unclear reasons). Overall, 66 patients (20.5%) were treated for pulmonary embolism.

Literature‐Derived Estimates of Posttest Probabilities of Pulmonary Embolism

Patients who have a low pretest probability of PE and a positive CTPA have a posttest probability of 41.6% under our estimate of CTPA test characteristics. Patients with moderate pretest probability have a posttest probability of 87.4% and patients with a high pretest probability will have a 98.5% probability of embolism with a positive scan. The traditional treatment threshold for PE is a posttest probability of 90%.22

Observed Versus Expected PE Rates and Subsequent Treatment

Only 9 of the 22 patients (41%) with a low pretest probability and a positive CTPA likely represent true‐positive emboli. However, clinicians chose to treat 21 of the 22 patients with this combination of pretest probability and imaging findings. Thus, 12 emboli would be considered possible false‐positive diagnoses. Similarly, in the moderate pretest probability group, 2 of 21 patients with moderate pretest probability and 0 of 13 patients with high pretest probability treated for PE had a possibly false‐positive diagnosis. Thus, in total, 25.4% (14 of 55) patients treated for PE had a possible false‐positive diagnosis of pulmonary embolism and may have been unnecessarily administered anticoagulants (Table 2). All patients who potentially had a false‐positive PE had either a low or moderate pretest probability of PE; in fact, the majority (57.1%) of patients with a low pretest probability of PE who were subsequently treated for PE likely had a false‐positive diagnosis.

Clinicians were more likely to overtreat a patient with a possible false‐positive CT scan than to withhold treatment from a patient with a possible false‐negative diagnosis. Using the same estimates of CTPA test characteristics, the incidence of possible false‐negative diagnosis of PE was 1.6% (4 possible false‐negative diagnoses among 254 patients with negative CTPA results who were not treated for PE.) All these patients had a high pretest probability of PE.

Sites and Subjects

Details of the sites, subjects, and methods used to collect patient‐level data in this analysis have been previously published.1 The study was performed at Moffitt‐Long Hospital and San Francisco General Hospital, teaching hospitals affiliated with the University of California San Francisco School of Medicine. At both sites, single‐detector CT scans were available 24 hours a day throughout the study period and were read by attending radiologists who specialized in thoracic imaging. We excluded patients whose CTPA was not completed as the initial test in the evaluation of suspected PE, those who underwent testing for any indication other than suspected acute PE, and those with incomplete medical records or technically inadequate CTPA.

We randomly selected 345 patients who underwent CTPA between January 1, 1998, and December 31, 2000, from the Radiology Department databases. One investigator (R.L.T.) then abstracted charts of all patients. For each subject, we collected data about history and clinical presentation, diagnostic impressions of the treating clinicians, treatments administered both before and after diagnostic testing, CTPA result, results of other diagnostic tests for PE, and final clinical diagnosis. During the study period, there were no institution‐ or department‐specific guidelines or decision aids available for the diagnosis of PE. Ventilation‐perfusion scan, lower extremity ultrasound, and pulmonary angiography were available, but highly sensitive D‐dimer assays were not in use. The study was approved by the Institutional Review Boards of both sites, and requirement for written informed consent from patients was waived.

Estimates of Pretest Probabilities of Pulmonary Embolism and CTPA Test Characteristics

Several prediction rules1820 generate clinical pretest probabilities for patients with suspected PE. We used the Wells score18 to assign a pretest probability of low, moderate, or high to each patient on the basis of the following clinical variables: leg swelling, hemoptysis, tachycardia, history of recent immobilization, history of prior DVT or PE, active malignancy, and lack of a more likely alternative diagnosis. We chose this rule as (unlike other prediction rules such as the Geneva rule20) the Wells score has been validated for hospitalized patients with suspected PE and does not require arterial blood gas measurements. The prevalence of PE reported in the evaluation of the Wells score was 3.4%, 27.8%, and 78.3% for low, moderate, and high pretest probabilities, respectively.18

As in our previous study,1 we assumed CTPA to be 90% sensitive and 95% specific based on published estimates.3, 17 These values correspond to a positive likelihood ratio of 18 and a negative likelihood ratio of 0.1.21 We chose these values as a best‐case estimate of the test characteristics of CTPA, although other studies have found less impressive results.7 Using these pretest probabilities and likelihood ratios, we then used Bayes' theorem (Figure 1) to calculate the range of expected posttest probabilities of pulmonary embolism.

Figure 1

Calculation of Posttest Probabilities and Comparison to Treatment Outcomes

For each pretest probability category, we used the posttest probabilities calculated above to determine the number of true‐positive pulmonary emboli, as follows: We then compared treatment decisions made by clinicians at our hospital to the calculated posttest probabilities and number of true‐positive diagnoses of PE. We considered the difference between the number of patients treated for PE and the number of true‐positive diagnoses of PE to represent possible false‐positive diagnoses. In a similar fashion, we determined the number of likely true‐negative diagnoses of PE and considered the difference between the number of patients not treated for PE and the number of true‐negative diagnoses to represent possible false‐negative diagnoses.

Patient Characteristics

After excluding 23 patients receiving anticoagulants for other indications prior to CTPA, the study cohort included 322 patients (57.7% female), with an average age of 58.6 years, of whom 20.5% had cancer and 4.5% had a prior history of thromboembolic disease. Scans were primarily ordered by the medicine service (47.7% of cases) and emergency department (22.9%). CTPA was the initial test for 9% of patients evaluated for suspected acute PE during the first 6 months of the study period, increasing to 83% by the end of 2000.1 The overall pretest probability distribution remained the same throughout the entire study period.1

Test Results and Treatment Decisions

Most patients in our cohort had a low (n = 184, 57.1%) or a moderate (n = 101, 31.4%) pretest probability of PE (Table 1). The likelihood of a positive CTPA increased as the pretest probability increased, but even among patients with high clinical risk, only 35.1% had positive CT scans. In total, scans were positive in 57 patients and negative in 265 patients. Clinicians treated 55 patients with a positive CTPA (96.5%); none of these patients underwent additional testing for DVT or PE after the imaging study. Among patients with a negative CTPA, 254 (95.8%) were not treated; none of the patients in whom anticoagulation was withheld underwent further testing, whereas the other 11 patients were treated on the basis of other tests (5 high‐probability ventilation‐perfusion scans, 3 positive leg ultrasounds, and 3 for unclear reasons). Overall, 66 patients (20.5%) were treated for pulmonary embolism.

Literature‐Derived Estimates of Posttest Probabilities of Pulmonary Embolism

Patients who have a low pretest probability of PE and a positive CTPA have a posttest probability of 41.6% under our estimate of CTPA test characteristics. Patients with moderate pretest probability have a posttest probability of 87.4% and patients with a high pretest probability will have a 98.5% probability of embolism with a positive scan. The traditional treatment threshold for PE is a posttest probability of 90%.22

Observed Versus Expected PE Rates and Subsequent Treatment

Only 9 of the 22 patients (41%) with a low pretest probability and a positive CTPA likely represent true‐positive emboli. However, clinicians chose to treat 21 of the 22 patients with this combination of pretest probability and imaging findings. Thus, 12 emboli would be considered possible false‐positive diagnoses. Similarly, in the moderate pretest probability group, 2 of 21 patients with moderate pretest probability and 0 of 13 patients with high pretest probability treated for PE had a possibly false‐positive diagnosis. Thus, in total, 25.4% (14 of 55) patients treated for PE had a possible false‐positive diagnosis of pulmonary embolism and may have been unnecessarily administered anticoagulants (Table 2). All patients who potentially had a false‐positive PE had either a low or moderate pretest probability of PE; in fact, the majority (57.1%) of patients with a low pretest probability of PE who were subsequently treated for PE likely had a false‐positive diagnosis.

Clinicians were more likely to overtreat a patient with a possible false‐positive CT scan than to withhold treatment from a patient with a possible false‐negative diagnosis. Using the same estimates of CTPA test characteristics, the incidence of possible false‐negative diagnosis of PE was 1.6% (4 possible false‐negative diagnoses among 254 patients with negative CTPA results who were not treated for PE.) All these patients had a high pretest probability of PE.

Sites and Subjects

Details of the sites, subjects, and methods used to collect patient‐level data in this analysis have been previously published.1 The study was performed at Moffitt‐Long Hospital and San Francisco General Hospital, teaching hospitals affiliated with the University of California San Francisco School of Medicine. At both sites, single‐detector CT scans were available 24 hours a day throughout the study period and were read by attending radiologists who specialized in thoracic imaging. We excluded patients whose CTPA was not completed as the initial test in the evaluation of suspected PE, those who underwent testing for any indication other than suspected acute PE, and those with incomplete medical records or technically inadequate CTPA.

We randomly selected 345 patients who underwent CTPA between January 1, 1998, and December 31, 2000, from the Radiology Department databases. One investigator (R.L.T.) then abstracted charts of all patients. For each subject, we collected data about history and clinical presentation, diagnostic impressions of the treating clinicians, treatments administered both before and after diagnostic testing, CTPA result, results of other diagnostic tests for PE, and final clinical diagnosis. During the study period, there were no institution‐ or department‐specific guidelines or decision aids available for the diagnosis of PE. Ventilation‐perfusion scan, lower extremity ultrasound, and pulmonary angiography were available, but highly sensitive D‐dimer assays were not in use. The study was approved by the Institutional Review Boards of both sites, and requirement for written informed consent from patients was waived.

Estimates of Pretest Probabilities of Pulmonary Embolism and CTPA Test Characteristics

Several prediction rules1820 generate clinical pretest probabilities for patients with suspected PE. We used the Wells score18 to assign a pretest probability of low, moderate, or high to each patient on the basis of the following clinical variables: leg swelling, hemoptysis, tachycardia, history of recent immobilization, history of prior DVT or PE, active malignancy, and lack of a more likely alternative diagnosis. We chose this rule as (unlike other prediction rules such as the Geneva rule20) the Wells score has been validated for hospitalized patients with suspected PE and does not require arterial blood gas measurements. The prevalence of PE reported in the evaluation of the Wells score was 3.4%, 27.8%, and 78.3% for low, moderate, and high pretest probabilities, respectively.18

As in our previous study,1 we assumed CTPA to be 90% sensitive and 95% specific based on published estimates.3, 17 These values correspond to a positive likelihood ratio of 18 and a negative likelihood ratio of 0.1.21 We chose these values as a best‐case estimate of the test characteristics of CTPA, although other studies have found less impressive results.7 Using these pretest probabilities and likelihood ratios, we then used Bayes' theorem (Figure 1) to calculate the range of expected posttest probabilities of pulmonary embolism.

Figure 1

Calculation of Posttest Probabilities and Comparison to Treatment Outcomes

For each pretest probability category, we used the posttest probabilities calculated above to determine the number of true‐positive pulmonary emboli, as follows: We then compared treatment decisions made by clinicians at our hospital to the calculated posttest probabilities and number of true‐positive diagnoses of PE. We considered the difference between the number of patients treated for PE and the number of true‐positive diagnoses of PE to represent possible false‐positive diagnoses. In a similar fashion, we determined the number of likely true‐negative diagnoses of PE and considered the difference between the number of patients not treated for PE and the number of true‐negative diagnoses to represent possible false‐negative diagnoses.

Patient Characteristics

After excluding 23 patients receiving anticoagulants for other indications prior to CTPA, the study cohort included 322 patients (57.7% female), with an average age of 58.6 years, of whom 20.5% had cancer and 4.5% had a prior history of thromboembolic disease. Scans were primarily ordered by the medicine service (47.7% of cases) and emergency department (22.9%). CTPA was the initial test for 9% of patients evaluated for suspected acute PE during the first 6 months of the study period, increasing to 83% by the end of 2000.1 The overall pretest probability distribution remained the same throughout the entire study period.1

Test Results and Treatment Decisions

Most patients in our cohort had a low (n = 184, 57.1%) or a moderate (n = 101, 31.4%) pretest probability of PE (Table 1). The likelihood of a positive CTPA increased as the pretest probability increased, but even among patients with high clinical risk, only 35.1% had positive CT scans. In total, scans were positive in 57 patients and negative in 265 patients. Clinicians treated 55 patients with a positive CTPA (96.5%); none of these patients underwent additional testing for DVT or PE after the imaging study. Among patients with a negative CTPA, 254 (95.8%) were not treated; none of the patients in whom anticoagulation was withheld underwent further testing, whereas the other 11 patients were treated on the basis of other tests (5 high‐probability ventilation‐perfusion scans, 3 positive leg ultrasounds, and 3 for unclear reasons). Overall, 66 patients (20.5%) were treated for pulmonary embolism.

Literature‐Derived Estimates of Posttest Probabilities of Pulmonary Embolism

Patients who have a low pretest probability of PE and a positive CTPA have a posttest probability of 41.6% under our estimate of CTPA test characteristics. Patients with moderate pretest probability have a posttest probability of 87.4% and patients with a high pretest probability will have a 98.5% probability of embolism with a positive scan. The traditional treatment threshold for PE is a posttest probability of 90%.22

Observed Versus Expected PE Rates and Subsequent Treatment

Only 9 of the 22 patients (41%) with a low pretest probability and a positive CTPA likely represent true‐positive emboli. However, clinicians chose to treat 21 of the 22 patients with this combination of pretest probability and imaging findings. Thus, 12 emboli would be considered possible false‐positive diagnoses. Similarly, in the moderate pretest probability group, 2 of 21 patients with moderate pretest probability and 0 of 13 patients with high pretest probability treated for PE had a possibly false‐positive diagnosis. Thus, in total, 25.4% (14 of 55) patients treated for PE had a possible false‐positive diagnosis of pulmonary embolism and may have been unnecessarily administered anticoagulants (Table 2). All patients who potentially had a false‐positive PE had either a low or moderate pretest probability of PE; in fact, the majority (57.1%) of patients with a low pretest probability of PE who were subsequently treated for PE likely had a false‐positive diagnosis.

Clinicians were more likely to overtreat a patient with a possible false‐positive CT scan than to withhold treatment from a patient with a possible false‐negative diagnosis. Using the same estimates of CTPA test characteristics, the incidence of possible false‐negative diagnosis of PE was 1.6% (4 possible false‐negative diagnoses among 254 patients with negative CTPA results who were not treated for PE.) All these patients had a high pretest probability of PE.