Eligibility Criteria

With help from an experienced biomedical librarian (C.D.S.), we searched PubMed, the Cumulative Index to Nursing and Allied Health Literature, Scopus, Cochrane Library, ClinicalTrials.gov, and Google Scholar from January 1980 through April 2015 (see Supporting Information in the online version of this article for the search terms and queries). We hand searched the reference lists of included articles and reviewed our personal libraries to identify additional relevant studies.

We included peer‐reviewed, original research studies published in English, Spanish, or French that addressed the questions outlined above. Eligible patient populations were children and adults admitted to hospital inpatient units and emergency departments (EDs). We excluded alarms in procedural suites or operating rooms (typically responded to by anesthesiologists already with the patient) because of the differences in environment of care, staff‐to‐patient ratio, and equipment. We included observational studies reporting the actionability of physiologic monitor alarms (ie, alarms warranting special attention or clinical intervention), as well as nurse responses to these alarms. We excluded studies focused on the effects of alarms unrelated to patient safety, such as families' and patients' stress, noise, or sleep disturbance. We included only intervention studies evaluating pragmatic interventions ready for clinical implementation (ie, not experimental devices or software algorithms).

Selection Process and Data Extraction

First, 2 authors screened the titles and abstracts of articles for eligibility. To maximize sensitivity, if at least 1 author considered the article relevant, the article proceeded to full‐text review. Second, the full texts of articles screened were independently reviewed by 2 authors in an unblinded fashion to determine their eligibility. Any disagreements concerning eligibility were resolved by team consensus. To assure consistency in eligibility determinations across the team, a core group of the authors (C.W.P, C.P.B., E.E., and V.V.G.) held a series of meetings to review and discuss each potentially eligible article and reach consensus on the final list of included articles. Two authors independently extracted the following characteristics from included studies: alarm review methods, analytic design, fidelity measurement, consideration of unintended adverse safety consequences, and key results. Reviewers were not blinded to journal, authors, or affiliations.

Synthesis of Results and Risk Assessment

Given the high degree of heterogeneity in methodology, we were unable to generate summary proportions of the observational studies or perform a meta‐analysis of the intervention studies. Thus, we organized the studies into clinically relevant categories and presented key aspects in tables. Due to the heterogeneity of the studies and the controversy surrounding quality scores,[5] we did not generate summary scores of study quality. Instead, we evaluated and reported key design elements that had the potential to bias the results. To recognize the more comprehensive studies in the field, we developed by consensus a set of characteristics that distinguished studies with lower risk of bias. These characteristics are shown and defined in Table 1.

For the purposes of this review, we defined nonactionable alarms as including both invalid (false) alarms that do not that accurately represent the physiologic status of the patient and alarms that are valid but do not warrant special attention or clinical intervention (nuisance alarms). We did not separate out invalid alarms due to the tremendous variation between studies in how validity was measured.

Study Selection

Search results produced 4629 articles (see the flow diagram in the Supporting Information in the online version of this article), of which 32 articles were eligible: 24 observational studies describing alarm characteristics and 8 studies describing interventions to reduce alarm frequency.

Observational Study Characteristics

Characteristics of included studies are shown in Table 1. Of the 24 observational studies,[7, 8, 9, 10, 11, 12, 13, 14, 15, 16, 17, 18, 19, 20, 21, 22, 23, 24, 25, 26, 27, 28, 29, 30] 15 included adult patients,[7, 8, 9, 10, 11, 12, 13, 14, 15, 16, 17, 18, 19, 20, 21] 7 included pediatric patients,[22, 23, 24, 25, 26, 27, 28] and 2 included both adult and pediatric patients.[29, 30] All were single‐hospital studies, except for 1 study by Chambrin and colleagues[10] that included 5 sites. The number of patient‐hours examined in each study ranged from 60 to 113,880.[7, 8, 9, 10, 11, 13, 14, 15, 16, 18, 19, 20, 21, 22, 23, 24, 25, 26, 27, 29, 30] Hospital settings included ICUs (n = 16),[9, 10, 11, 13, 14, 16, 17, 18, 19, 22, 23, 24, 25, 26, 27, 29] general wards (n = 5),[12, 15, 20, 22, 28] EDs (n = 2),[7, 21] postanesthesia care unit (PACU) (n = 1),[30] and cardiac care unit (CCU) (n = 1).[8] Studies varied in the type of physiologic signals recorded and data collection methods, ranging from direct observation by a nurse who was simultaneously caring for patients[29] to video recording with expert review.[14, 19, 22] Four observational studies met the criteria for lower risk of bias.[11, 14, 15, 22]

Intervention Study Characteristics

Of the 8 intervention studies, 7 included adult patients,[31, 32, 33, 34, 35, 36, 37] and 1 included pediatric patients.[38] All were single‐hospital studies; 6 were quasi‐experimental[31, 33, 34, 35, 37, 38] and 2 were experimental.[32, 36] Settings included progressive care units (n = 3),[33, 34, 35] CCUs (n = 3),[32, 33, 37] wards (n = 2),[31, 38] PACU (n = 1),[36] and a step‐down unit (n = 1).[32] All except 1 study[32] used the monitoring system to record alarm data. Several studies evaluated multicomponent interventions that included combinations of the following: widening alarm parameters,[31, 35, 36, 37, 38] instituting alarm delays,[31, 34, 36, 38] reconfiguring alarm acuity,[35, 37] use of secondary notifications,[34] daily change of electrocardiographic electrodes or use of disposable electrocardiographic wires,[32, 33, 38] universal monitoring in high‐risk populations,[31] and timely discontinuation of monitoring in low‐risk populations.[38] Four intervention studies met our prespecified lower risk of bias criteria.[31, 32, 36, 38]

Proportion of Alarms Considered Actionable

Results of the observational studies are provided in Table 2. The proportion of alarms that were actionable was <1% to 26% in adult ICU settings,[9, 10, 11, 13, 14, 16, 17, 19] 20% to 36% in adult ward settings,[12, 15, 20] 17% in a mixed adult and pediatric PACU setting,[30] 3% to 13% in pediatric ICU settings,[22, 23, 24, 25, 26] and 1% in a pediatric ward setting.[22]

Relationship Between Alarm Exposure and Response Time

Whereas 9 studies addressed response time,[8, 12, 17, 18, 20, 21, 22, 27, 28] only 2 evaluated the relationship between alarm burden and nurse response time.[20, 22] Voepel‐Lewis and colleagues found that nurse responses were slower to patients with the highest quartile of alarms (57.6 seconds) compared to those with the lowest (45.4 seconds) or medium (42.3 seconds) quartiles of alarms on an adult ward (P = 0.046). They did not find an association between false alarm exposure and response time.[20] Bonafide and colleagues found incremental increases in response time as the number of nonactionable alarms in the preceding 120 minutes increased (P < 0.001 in the pediatric ICU, P = 0.009 on the pediatric ward).[22]

Interventions Effective in Reducing Alarms

Results of the 8 intervention studies are provided in Table 3. Three studies evaluated single interventions;[32, 33, 36] the remainder of the studies tested interventions with multiple components such that it was impossible to separate the effect of each component. Below, we have summarized study results, arranged by component. Because only 1 study focused on pediatric patients,[38] results from pediatric and adult settings are combined.

Widening alarm parameter default settings was evaluated in 5 studies:[31, 35, 36, 37, 38] 1 single intervention randomized controlled trial (RCT),[36] and 4 multiple‐intervention, quasi‐experimental studies.[31, 35, 37, 38] In the RCT, using a lower SpO₂ limit of 85% instead of the standard 90% resulted in 61% fewer alarms. In the 4 multiple intervention studies, 1 study reported significant reductions in alarm rates (P < 0.001),[37] 1 study did not report preintervention alarm rates but reported a postintervention alarm rate of 4 alarms per patient‐day,[31] and 2 studies reported reductions in alarm rates but did not report any statistical testing.[35, 38] Of the 3 studies examining patient safety, 1 study with universal monitoring reported fewer rescue events and transfers to the ICU postimplementation,[31] 1 study reported no missed acute decompensations,[38] and 1 study (the RCT) reported significantly more true hypoxemia events (P = 0.001).[36]

Alarm delays were evaluated in 4 studies:[31, 34, 36, 38] 3 multiple‐intervention, quasi‐experimental studies[31, 34, 38] and 1 retrospective analysis of data from an RCT.[36] One study combined alarm delays with widening defaults in a universal monitoring strategy and reported a postintervention alarm rate of 4 alarms per patient.[31] Another study evaluated delays as part of a secondary notification pager system and found a negatively sloping regression line that suggested a decreasing alarm rate, but did not report statistical testing.[34] The third study reported a reduction in alarm rates but did not report statistical testing.[38] The RCT compared the impact of a hypothetical 15‐second alarm delay to that of a lower SpO₂ limit reduction and reported a similar reduction in alarms.[36] Of the 4 studies examining patient safety, 1 study with universal monitoring reported improvements,[31] 2 studies reported no adverse outcomes,[35, 38] and the retrospective analysis of data from the RCT reported the theoretical adverse outcome of delayed detection of sudden, severe desaturations.[36]

Reconfiguring alarm acuity was evaluated in 2 studies, both of which were multiple‐intervention quasi‐experimental studies.[35, 37] Both showed reductions in alarm rates: 1 was significant without increasing adverse events (P < 0.001),[37] and the other did not report statistical testing or safety outcomes.[35]

Secondary notification of nurses using pagers was the main intervention component of 1 study incorporating delays between the alarms and the alarm pages.[34] As mentioned above, a negatively sloping regression line was displayed, but no statistical testing or safety outcomes were reported.

Disposable electrocardiographic lead wires or daily electrode changes were evaluated in 3 studies:[32, 33, 38] 1 single intervention cluster‐randomized trial[32] and 2 quasi‐experimental studies.[33, 38] In the cluster‐randomized trial, disposable lead wires were compared to reusable lead wires, with disposable lead wires having significantly fewer technical alarms for lead signal failures (P = 0.03) but a similar number of monitoring artifact alarms (P = 0.44).[32] In a single‐intervention, quasi‐experimental study, daily electrode change showed a reduction in alarms, but no statistical testing was reported.[33] One multiple‐intervention, quasi‐experimental study incorporating daily electrode change showed fewer alarms without statistical testing.[38] Of the 2 studies examining patient safety, both reported no adverse outcomes.[32, 38]

Limitations of This Review and the Underlying Body of Work

There are limitations to this systematic review and its underlying body of work. With respect to our approach to this systematic review, we focused only on monitor alarms. Numerous other medical devices generate alarms in the patient‐care environment that also can contribute to alarm fatigue and deserve equally rigorous evaluation. With respect to the underlying body of work, the quality of individual studies was generally low. For example, determinations of alarm actionability were often made by a single rater without evaluation of the reliability or validity of these determinations, and statistical testing was often missing. There were also limitations specific to intervention studies, including evaluation of nongeneralizable patient populations, failure to measure the fidelity of the interventions, inadequate measures of intervention safety, and failure to statistically evaluate alarm reductions. Finally, though not necessarily a limitation, several studies were conducted by authors involved in or funded by the medical device industry.[11, 15, 19, 31, 32] This has the potential to introduce bias, although we have no indication that the quality of the science was adversely impacted.

Moving forward, the research agenda for physiologic monitor alarms should include the following: (1) more intensive focus on evaluating the relationship between alarm exposure and response time with analysis of important mediating factors that may promote or prevent alarm fatigue, (2) emphasis on studying interventions aimed at improving alarm management using rigorous designs such as cluster‐randomized trials and trials randomized by individual participant, (3) monitoring and reporting clinically meaningful balancing measures that represent unintended consequences of disabling or delaying potentially important alarms and possibly reducing the clinicians' ability to detect true patient deterioration and intervene in a timely manner, and (4) support for transparent academicindustry partnerships to evaluate new alarm technology in real‐world settings. As evidence‐based interventions emerge, there will be new opportunities to study different implementation strategies of these interventions to optimize effectiveness.

Eligibility Criteria

With help from an experienced biomedical librarian (C.D.S.), we searched PubMed, the Cumulative Index to Nursing and Allied Health Literature, Scopus, Cochrane Library, ClinicalTrials.gov, and Google Scholar from January 1980 through April 2015 (see Supporting Information in the online version of this article for the search terms and queries). We hand searched the reference lists of included articles and reviewed our personal libraries to identify additional relevant studies.

We included peer‐reviewed, original research studies published in English, Spanish, or French that addressed the questions outlined above. Eligible patient populations were children and adults admitted to hospital inpatient units and emergency departments (EDs). We excluded alarms in procedural suites or operating rooms (typically responded to by anesthesiologists already with the patient) because of the differences in environment of care, staff‐to‐patient ratio, and equipment. We included observational studies reporting the actionability of physiologic monitor alarms (ie, alarms warranting special attention or clinical intervention), as well as nurse responses to these alarms. We excluded studies focused on the effects of alarms unrelated to patient safety, such as families' and patients' stress, noise, or sleep disturbance. We included only intervention studies evaluating pragmatic interventions ready for clinical implementation (ie, not experimental devices or software algorithms).

Selection Process and Data Extraction

First, 2 authors screened the titles and abstracts of articles for eligibility. To maximize sensitivity, if at least 1 author considered the article relevant, the article proceeded to full‐text review. Second, the full texts of articles screened were independently reviewed by 2 authors in an unblinded fashion to determine their eligibility. Any disagreements concerning eligibility were resolved by team consensus. To assure consistency in eligibility determinations across the team, a core group of the authors (C.W.P, C.P.B., E.E., and V.V.G.) held a series of meetings to review and discuss each potentially eligible article and reach consensus on the final list of included articles. Two authors independently extracted the following characteristics from included studies: alarm review methods, analytic design, fidelity measurement, consideration of unintended adverse safety consequences, and key results. Reviewers were not blinded to journal, authors, or affiliations.

Synthesis of Results and Risk Assessment

Given the high degree of heterogeneity in methodology, we were unable to generate summary proportions of the observational studies or perform a meta‐analysis of the intervention studies. Thus, we organized the studies into clinically relevant categories and presented key aspects in tables. Due to the heterogeneity of the studies and the controversy surrounding quality scores,[5] we did not generate summary scores of study quality. Instead, we evaluated and reported key design elements that had the potential to bias the results. To recognize the more comprehensive studies in the field, we developed by consensus a set of characteristics that distinguished studies with lower risk of bias. These characteristics are shown and defined in Table 1.

For the purposes of this review, we defined nonactionable alarms as including both invalid (false) alarms that do not that accurately represent the physiologic status of the patient and alarms that are valid but do not warrant special attention or clinical intervention (nuisance alarms). We did not separate out invalid alarms due to the tremendous variation between studies in how validity was measured.

Study Selection

Search results produced 4629 articles (see the flow diagram in the Supporting Information in the online version of this article), of which 32 articles were eligible: 24 observational studies describing alarm characteristics and 8 studies describing interventions to reduce alarm frequency.

Observational Study Characteristics

Characteristics of included studies are shown in Table 1. Of the 24 observational studies,[7, 8, 9, 10, 11, 12, 13, 14, 15, 16, 17, 18, 19, 20, 21, 22, 23, 24, 25, 26, 27, 28, 29, 30] 15 included adult patients,[7, 8, 9, 10, 11, 12, 13, 14, 15, 16, 17, 18, 19, 20, 21] 7 included pediatric patients,[22, 23, 24, 25, 26, 27, 28] and 2 included both adult and pediatric patients.[29, 30] All were single‐hospital studies, except for 1 study by Chambrin and colleagues[10] that included 5 sites. The number of patient‐hours examined in each study ranged from 60 to 113,880.[7, 8, 9, 10, 11, 13, 14, 15, 16, 18, 19, 20, 21, 22, 23, 24, 25, 26, 27, 29, 30] Hospital settings included ICUs (n = 16),[9, 10, 11, 13, 14, 16, 17, 18, 19, 22, 23, 24, 25, 26, 27, 29] general wards (n = 5),[12, 15, 20, 22, 28] EDs (n = 2),[7, 21] postanesthesia care unit (PACU) (n = 1),[30] and cardiac care unit (CCU) (n = 1).[8] Studies varied in the type of physiologic signals recorded and data collection methods, ranging from direct observation by a nurse who was simultaneously caring for patients[29] to video recording with expert review.[14, 19, 22] Four observational studies met the criteria for lower risk of bias.[11, 14, 15, 22]

Intervention Study Characteristics

Of the 8 intervention studies, 7 included adult patients,[31, 32, 33, 34, 35, 36, 37] and 1 included pediatric patients.[38] All were single‐hospital studies; 6 were quasi‐experimental[31, 33, 34, 35, 37, 38] and 2 were experimental.[32, 36] Settings included progressive care units (n = 3),[33, 34, 35] CCUs (n = 3),[32, 33, 37] wards (n = 2),[31, 38] PACU (n = 1),[36] and a step‐down unit (n = 1).[32] All except 1 study[32] used the monitoring system to record alarm data. Several studies evaluated multicomponent interventions that included combinations of the following: widening alarm parameters,[31, 35, 36, 37, 38] instituting alarm delays,[31, 34, 36, 38] reconfiguring alarm acuity,[35, 37] use of secondary notifications,[34] daily change of electrocardiographic electrodes or use of disposable electrocardiographic wires,[32, 33, 38] universal monitoring in high‐risk populations,[31] and timely discontinuation of monitoring in low‐risk populations.[38] Four intervention studies met our prespecified lower risk of bias criteria.[31, 32, 36, 38]

Proportion of Alarms Considered Actionable

Results of the observational studies are provided in Table 2. The proportion of alarms that were actionable was <1% to 26% in adult ICU settings,[9, 10, 11, 13, 14, 16, 17, 19] 20% to 36% in adult ward settings,[12, 15, 20] 17% in a mixed adult and pediatric PACU setting,[30] 3% to 13% in pediatric ICU settings,[22, 23, 24, 25, 26] and 1% in a pediatric ward setting.[22]

Relationship Between Alarm Exposure and Response Time

Whereas 9 studies addressed response time,[8, 12, 17, 18, 20, 21, 22, 27, 28] only 2 evaluated the relationship between alarm burden and nurse response time.[20, 22] Voepel‐Lewis and colleagues found that nurse responses were slower to patients with the highest quartile of alarms (57.6 seconds) compared to those with the lowest (45.4 seconds) or medium (42.3 seconds) quartiles of alarms on an adult ward (P = 0.046). They did not find an association between false alarm exposure and response time.[20] Bonafide and colleagues found incremental increases in response time as the number of nonactionable alarms in the preceding 120 minutes increased (P < 0.001 in the pediatric ICU, P = 0.009 on the pediatric ward).[22]

Interventions Effective in Reducing Alarms

Results of the 8 intervention studies are provided in Table 3. Three studies evaluated single interventions;[32, 33, 36] the remainder of the studies tested interventions with multiple components such that it was impossible to separate the effect of each component. Below, we have summarized study results, arranged by component. Because only 1 study focused on pediatric patients,[38] results from pediatric and adult settings are combined.

Widening alarm parameter default settings was evaluated in 5 studies:[31, 35, 36, 37, 38] 1 single intervention randomized controlled trial (RCT),[36] and 4 multiple‐intervention, quasi‐experimental studies.[31, 35, 37, 38] In the RCT, using a lower SpO₂ limit of 85% instead of the standard 90% resulted in 61% fewer alarms. In the 4 multiple intervention studies, 1 study reported significant reductions in alarm rates (P < 0.001),[37] 1 study did not report preintervention alarm rates but reported a postintervention alarm rate of 4 alarms per patient‐day,[31] and 2 studies reported reductions in alarm rates but did not report any statistical testing.[35, 38] Of the 3 studies examining patient safety, 1 study with universal monitoring reported fewer rescue events and transfers to the ICU postimplementation,[31] 1 study reported no missed acute decompensations,[38] and 1 study (the RCT) reported significantly more true hypoxemia events (P = 0.001).[36]

Alarm delays were evaluated in 4 studies:[31, 34, 36, 38] 3 multiple‐intervention, quasi‐experimental studies[31, 34, 38] and 1 retrospective analysis of data from an RCT.[36] One study combined alarm delays with widening defaults in a universal monitoring strategy and reported a postintervention alarm rate of 4 alarms per patient.[31] Another study evaluated delays as part of a secondary notification pager system and found a negatively sloping regression line that suggested a decreasing alarm rate, but did not report statistical testing.[34] The third study reported a reduction in alarm rates but did not report statistical testing.[38] The RCT compared the impact of a hypothetical 15‐second alarm delay to that of a lower SpO₂ limit reduction and reported a similar reduction in alarms.[36] Of the 4 studies examining patient safety, 1 study with universal monitoring reported improvements,[31] 2 studies reported no adverse outcomes,[35, 38] and the retrospective analysis of data from the RCT reported the theoretical adverse outcome of delayed detection of sudden, severe desaturations.[36]

Reconfiguring alarm acuity was evaluated in 2 studies, both of which were multiple‐intervention quasi‐experimental studies.[35, 37] Both showed reductions in alarm rates: 1 was significant without increasing adverse events (P < 0.001),[37] and the other did not report statistical testing or safety outcomes.[35]

Secondary notification of nurses using pagers was the main intervention component of 1 study incorporating delays between the alarms and the alarm pages.[34] As mentioned above, a negatively sloping regression line was displayed, but no statistical testing or safety outcomes were reported.

Disposable electrocardiographic lead wires or daily electrode changes were evaluated in 3 studies:[32, 33, 38] 1 single intervention cluster‐randomized trial[32] and 2 quasi‐experimental studies.[33, 38] In the cluster‐randomized trial, disposable lead wires were compared to reusable lead wires, with disposable lead wires having significantly fewer technical alarms for lead signal failures (P = 0.03) but a similar number of monitoring artifact alarms (P = 0.44).[32] In a single‐intervention, quasi‐experimental study, daily electrode change showed a reduction in alarms, but no statistical testing was reported.[33] One multiple‐intervention, quasi‐experimental study incorporating daily electrode change showed fewer alarms without statistical testing.[38] Of the 2 studies examining patient safety, both reported no adverse outcomes.[32, 38]

Limitations of This Review and the Underlying Body of Work

There are limitations to this systematic review and its underlying body of work. With respect to our approach to this systematic review, we focused only on monitor alarms. Numerous other medical devices generate alarms in the patient‐care environment that also can contribute to alarm fatigue and deserve equally rigorous evaluation. With respect to the underlying body of work, the quality of individual studies was generally low. For example, determinations of alarm actionability were often made by a single rater without evaluation of the reliability or validity of these determinations, and statistical testing was often missing. There were also limitations specific to intervention studies, including evaluation of nongeneralizable patient populations, failure to measure the fidelity of the interventions, inadequate measures of intervention safety, and failure to statistically evaluate alarm reductions. Finally, though not necessarily a limitation, several studies were conducted by authors involved in or funded by the medical device industry.[11, 15, 19, 31, 32] This has the potential to introduce bias, although we have no indication that the quality of the science was adversely impacted.

Moving forward, the research agenda for physiologic monitor alarms should include the following: (1) more intensive focus on evaluating the relationship between alarm exposure and response time with analysis of important mediating factors that may promote or prevent alarm fatigue, (2) emphasis on studying interventions aimed at improving alarm management using rigorous designs such as cluster‐randomized trials and trials randomized by individual participant, (3) monitoring and reporting clinically meaningful balancing measures that represent unintended consequences of disabling or delaying potentially important alarms and possibly reducing the clinicians' ability to detect true patient deterioration and intervene in a timely manner, and (4) support for transparent academicindustry partnerships to evaluate new alarm technology in real‐world settings. As evidence‐based interventions emerge, there will be new opportunities to study different implementation strategies of these interventions to optimize effectiveness.

Eligibility Criteria

With help from an experienced biomedical librarian (C.D.S.), we searched PubMed, the Cumulative Index to Nursing and Allied Health Literature, Scopus, Cochrane Library, ClinicalTrials.gov, and Google Scholar from January 1980 through April 2015 (see Supporting Information in the online version of this article for the search terms and queries). We hand searched the reference lists of included articles and reviewed our personal libraries to identify additional relevant studies.

We included peer‐reviewed, original research studies published in English, Spanish, or French that addressed the questions outlined above. Eligible patient populations were children and adults admitted to hospital inpatient units and emergency departments (EDs). We excluded alarms in procedural suites or operating rooms (typically responded to by anesthesiologists already with the patient) because of the differences in environment of care, staff‐to‐patient ratio, and equipment. We included observational studies reporting the actionability of physiologic monitor alarms (ie, alarms warranting special attention or clinical intervention), as well as nurse responses to these alarms. We excluded studies focused on the effects of alarms unrelated to patient safety, such as families' and patients' stress, noise, or sleep disturbance. We included only intervention studies evaluating pragmatic interventions ready for clinical implementation (ie, not experimental devices or software algorithms).

Selection Process and Data Extraction

First, 2 authors screened the titles and abstracts of articles for eligibility. To maximize sensitivity, if at least 1 author considered the article relevant, the article proceeded to full‐text review. Second, the full texts of articles screened were independently reviewed by 2 authors in an unblinded fashion to determine their eligibility. Any disagreements concerning eligibility were resolved by team consensus. To assure consistency in eligibility determinations across the team, a core group of the authors (C.W.P, C.P.B., E.E., and V.V.G.) held a series of meetings to review and discuss each potentially eligible article and reach consensus on the final list of included articles. Two authors independently extracted the following characteristics from included studies: alarm review methods, analytic design, fidelity measurement, consideration of unintended adverse safety consequences, and key results. Reviewers were not blinded to journal, authors, or affiliations.

Synthesis of Results and Risk Assessment

Given the high degree of heterogeneity in methodology, we were unable to generate summary proportions of the observational studies or perform a meta‐analysis of the intervention studies. Thus, we organized the studies into clinically relevant categories and presented key aspects in tables. Due to the heterogeneity of the studies and the controversy surrounding quality scores,[5] we did not generate summary scores of study quality. Instead, we evaluated and reported key design elements that had the potential to bias the results. To recognize the more comprehensive studies in the field, we developed by consensus a set of characteristics that distinguished studies with lower risk of bias. These characteristics are shown and defined in Table 1.

For the purposes of this review, we defined nonactionable alarms as including both invalid (false) alarms that do not that accurately represent the physiologic status of the patient and alarms that are valid but do not warrant special attention or clinical intervention (nuisance alarms). We did not separate out invalid alarms due to the tremendous variation between studies in how validity was measured.

Study Selection

Search results produced 4629 articles (see the flow diagram in the Supporting Information in the online version of this article), of which 32 articles were eligible: 24 observational studies describing alarm characteristics and 8 studies describing interventions to reduce alarm frequency.

Observational Study Characteristics

Characteristics of included studies are shown in Table 1. Of the 24 observational studies,[7, 8, 9, 10, 11, 12, 13, 14, 15, 16, 17, 18, 19, 20, 21, 22, 23, 24, 25, 26, 27, 28, 29, 30] 15 included adult patients,[7, 8, 9, 10, 11, 12, 13, 14, 15, 16, 17, 18, 19, 20, 21] 7 included pediatric patients,[22, 23, 24, 25, 26, 27, 28] and 2 included both adult and pediatric patients.[29, 30] All were single‐hospital studies, except for 1 study by Chambrin and colleagues[10] that included 5 sites. The number of patient‐hours examined in each study ranged from 60 to 113,880.[7, 8, 9, 10, 11, 13, 14, 15, 16, 18, 19, 20, 21, 22, 23, 24, 25, 26, 27, 29, 30] Hospital settings included ICUs (n = 16),[9, 10, 11, 13, 14, 16, 17, 18, 19, 22, 23, 24, 25, 26, 27, 29] general wards (n = 5),[12, 15, 20, 22, 28] EDs (n = 2),[7, 21] postanesthesia care unit (PACU) (n = 1),[30] and cardiac care unit (CCU) (n = 1).[8] Studies varied in the type of physiologic signals recorded and data collection methods, ranging from direct observation by a nurse who was simultaneously caring for patients[29] to video recording with expert review.[14, 19, 22] Four observational studies met the criteria for lower risk of bias.[11, 14, 15, 22]

Intervention Study Characteristics

Of the 8 intervention studies, 7 included adult patients,[31, 32, 33, 34, 35, 36, 37] and 1 included pediatric patients.[38] All were single‐hospital studies; 6 were quasi‐experimental[31, 33, 34, 35, 37, 38] and 2 were experimental.[32, 36] Settings included progressive care units (n = 3),[33, 34, 35] CCUs (n = 3),[32, 33, 37] wards (n = 2),[31, 38] PACU (n = 1),[36] and a step‐down unit (n = 1).[32] All except 1 study[32] used the monitoring system to record alarm data. Several studies evaluated multicomponent interventions that included combinations of the following: widening alarm parameters,[31, 35, 36, 37, 38] instituting alarm delays,[31, 34, 36, 38] reconfiguring alarm acuity,[35, 37] use of secondary notifications,[34] daily change of electrocardiographic electrodes or use of disposable electrocardiographic wires,[32, 33, 38] universal monitoring in high‐risk populations,[31] and timely discontinuation of monitoring in low‐risk populations.[38] Four intervention studies met our prespecified lower risk of bias criteria.[31, 32, 36, 38]

Proportion of Alarms Considered Actionable

Results of the observational studies are provided in Table 2. The proportion of alarms that were actionable was <1% to 26% in adult ICU settings,[9, 10, 11, 13, 14, 16, 17, 19] 20% to 36% in adult ward settings,[12, 15, 20] 17% in a mixed adult and pediatric PACU setting,[30] 3% to 13% in pediatric ICU settings,[22, 23, 24, 25, 26] and 1% in a pediatric ward setting.[22]

Relationship Between Alarm Exposure and Response Time

Whereas 9 studies addressed response time,[8, 12, 17, 18, 20, 21, 22, 27, 28] only 2 evaluated the relationship between alarm burden and nurse response time.[20, 22] Voepel‐Lewis and colleagues found that nurse responses were slower to patients with the highest quartile of alarms (57.6 seconds) compared to those with the lowest (45.4 seconds) or medium (42.3 seconds) quartiles of alarms on an adult ward (P = 0.046). They did not find an association between false alarm exposure and response time.[20] Bonafide and colleagues found incremental increases in response time as the number of nonactionable alarms in the preceding 120 minutes increased (P < 0.001 in the pediatric ICU, P = 0.009 on the pediatric ward).[22]

Interventions Effective in Reducing Alarms

Results of the 8 intervention studies are provided in Table 3. Three studies evaluated single interventions;[32, 33, 36] the remainder of the studies tested interventions with multiple components such that it was impossible to separate the effect of each component. Below, we have summarized study results, arranged by component. Because only 1 study focused on pediatric patients,[38] results from pediatric and adult settings are combined.

Widening alarm parameter default settings was evaluated in 5 studies:[31, 35, 36, 37, 38] 1 single intervention randomized controlled trial (RCT),[36] and 4 multiple‐intervention, quasi‐experimental studies.[31, 35, 37, 38] In the RCT, using a lower SpO₂ limit of 85% instead of the standard 90% resulted in 61% fewer alarms. In the 4 multiple intervention studies, 1 study reported significant reductions in alarm rates (P < 0.001),[37] 1 study did not report preintervention alarm rates but reported a postintervention alarm rate of 4 alarms per patient‐day,[31] and 2 studies reported reductions in alarm rates but did not report any statistical testing.[35, 38] Of the 3 studies examining patient safety, 1 study with universal monitoring reported fewer rescue events and transfers to the ICU postimplementation,[31] 1 study reported no missed acute decompensations,[38] and 1 study (the RCT) reported significantly more true hypoxemia events (P = 0.001).[36]

Alarm delays were evaluated in 4 studies:[31, 34, 36, 38] 3 multiple‐intervention, quasi‐experimental studies[31, 34, 38] and 1 retrospective analysis of data from an RCT.[36] One study combined alarm delays with widening defaults in a universal monitoring strategy and reported a postintervention alarm rate of 4 alarms per patient.[31] Another study evaluated delays as part of a secondary notification pager system and found a negatively sloping regression line that suggested a decreasing alarm rate, but did not report statistical testing.[34] The third study reported a reduction in alarm rates but did not report statistical testing.[38] The RCT compared the impact of a hypothetical 15‐second alarm delay to that of a lower SpO₂ limit reduction and reported a similar reduction in alarms.[36] Of the 4 studies examining patient safety, 1 study with universal monitoring reported improvements,[31] 2 studies reported no adverse outcomes,[35, 38] and the retrospective analysis of data from the RCT reported the theoretical adverse outcome of delayed detection of sudden, severe desaturations.[36]

Reconfiguring alarm acuity was evaluated in 2 studies, both of which were multiple‐intervention quasi‐experimental studies.[35, 37] Both showed reductions in alarm rates: 1 was significant without increasing adverse events (P < 0.001),[37] and the other did not report statistical testing or safety outcomes.[35]

Secondary notification of nurses using pagers was the main intervention component of 1 study incorporating delays between the alarms and the alarm pages.[34] As mentioned above, a negatively sloping regression line was displayed, but no statistical testing or safety outcomes were reported.

Disposable electrocardiographic lead wires or daily electrode changes were evaluated in 3 studies:[32, 33, 38] 1 single intervention cluster‐randomized trial[32] and 2 quasi‐experimental studies.[33, 38] In the cluster‐randomized trial, disposable lead wires were compared to reusable lead wires, with disposable lead wires having significantly fewer technical alarms for lead signal failures (P = 0.03) but a similar number of monitoring artifact alarms (P = 0.44).[32] In a single‐intervention, quasi‐experimental study, daily electrode change showed a reduction in alarms, but no statistical testing was reported.[33] One multiple‐intervention, quasi‐experimental study incorporating daily electrode change showed fewer alarms without statistical testing.[38] Of the 2 studies examining patient safety, both reported no adverse outcomes.[32, 38]

Limitations of This Review and the Underlying Body of Work

There are limitations to this systematic review and its underlying body of work. With respect to our approach to this systematic review, we focused only on monitor alarms. Numerous other medical devices generate alarms in the patient‐care environment that also can contribute to alarm fatigue and deserve equally rigorous evaluation. With respect to the underlying body of work, the quality of individual studies was generally low. For example, determinations of alarm actionability were often made by a single rater without evaluation of the reliability or validity of these determinations, and statistical testing was often missing. There were also limitations specific to intervention studies, including evaluation of nongeneralizable patient populations, failure to measure the fidelity of the interventions, inadequate measures of intervention safety, and failure to statistically evaluate alarm reductions. Finally, though not necessarily a limitation, several studies were conducted by authors involved in or funded by the medical device industry.[11, 15, 19, 31, 32] This has the potential to introduce bias, although we have no indication that the quality of the science was adversely impacted.

Moving forward, the research agenda for physiologic monitor alarms should include the following: (1) more intensive focus on evaluating the relationship between alarm exposure and response time with analysis of important mediating factors that may promote or prevent alarm fatigue, (2) emphasis on studying interventions aimed at improving alarm management using rigorous designs such as cluster‐randomized trials and trials randomized by individual participant, (3) monitoring and reporting clinically meaningful balancing measures that represent unintended consequences of disabling or delaying potentially important alarms and possibly reducing the clinicians' ability to detect true patient deterioration and intervene in a timely manner, and (4) support for transparent academicindustry partnerships to evaluate new alarm technology in real‐world settings. As evidence‐based interventions emerge, there will be new opportunities to study different implementation strategies of these interventions to optimize effectiveness.

Study Cohort

We identified all smokers aged 40 years hospitalized between 2005 and 2012 with either a primary discharge diagnosis of COPD based on International Classification of Diseases, 9th Revision codes (491, 492, 493.2, and 496) or an admission diagnosis from the text of the admit notes indicating an exacerbation of COPD. We limited to patients aged 40 years to improve the specificity of the diagnosis of COPD, and we selected the first hospitalization that met inclusion criteria. We excluded subjects who died within 6 months of discharge (Figure 1).

Figure 1

To establish tobacco status, we built on previously developed and validated methodology,[11] and performed truncated natural language processing using phrases in the medical record that reflected patients' tobacco status, querying all notes from the day of admission up to 6 months prior. If no tobacco status was indicated in the notes, we identified the status encoded by the most recent health factor. We manually examined the results of the natural language processing and the determination of health factors to confirm the tobacco status. Manual review was undertaken by 1 of 2 trained study personnel. In the case of an ambiguous or contradictory status, an additional team member reviewed the information to attempt to make a determination. If no determination could be made, the record was coded to unknown. This method allowed us to identify a baseline status for all but 77 of the 3580 patients admitted for COPD.

Outcome and Exposure

The outcome was tobacco status at 6 to 12 months after discharge. Using the same methods developed for identification of baseline smoking status, we obtained smoking status for each subject up to 12 months postdischarge. If multiple notes and encounters were available indicating smoking status, we chose the latest within 12 months of discharge. Subjects lacking a follow‐up status were presumed to be smokers, a common assumption.[12] The 6 to 12month time horizon was chosen as these are the most common time points used to examine a sustained change in tobacco status,[13, 14, 15] and allowed for adequate time for treatment and clinical follow‐up.

Our primary exposure was any smoking cessation medication or combination dispensed within 90 days of discharge. This time horizon for treatment was chosen due to recent studies indicating this is a meaningful period for postdischarge treatment.[14] We assessed the use of nicotine patch, short‐acting nicotine, varenicline, buproprion, or any combination. Accurate data on the prescription and dispensing of these medications were available from the VA pharmacy record. Secondary exposure was the choice of medication dispensed among treated patients. We assessed additional exposures including receipt of cessation medications within 48 hours of discharge, treatment in the year prior to admission, and predischarge counseling. Predischarge counseling was determined as having occurred if nurses documented that they completed a discharge process focused on smoking cessation. Referral to a quit line is part of this process; however, due to the confidential nature of these interactions, generally low use of this service, and lack of linkage to the VA electronic health record, it was not considered in the analysis.

Confounders

Potential confounders were assessed in the year prior to admission up to discharge from the index hospitalization, with the use of mechanical or noninvasive ventilation assessed during the hospitalization. We adjusted for variables chosen a priori for their known or expected association with smoking cessation including demographics, Charlson Comorbidity Index,[16] markers of COPD severity (need for invasive or noninvasive mechanical ventilation during index hospitalization, use of oral steroids, long‐acting inhaled bronchodilators, and/or canister count of short‐acting bronchodilators in the year prior to admission), history of drug or alcohol abuse, homelessness, depression, psychosis, post‐traumatic stress disorder, lung cancer, coronary artery disease, and under‐ or overweight status. Nurse‐based counseling prior to discharge was included as a variable for adjustment for our primary and secondary predictors to assess the influence of pharmacotherapy specifically. Due to 3.1% missingness in body mass index, multiple imputation with chained equations was used to impute missing values, with 10 imputations performed. The imputation was performed using a linear regression model containing all variables included in the final model, grouped by facility.

Statistical Analysis

All analyses were performed using Stata 13 (StataCorp, College Station, TX) software. ² tests and t tests were used to assess for unadjusted bivariate associations. Using the pooled imputed datasets, we performed multivariable logistic regression to compare odds ratios for a change in smoking status, adjusting the estimates of coefficients and standard errors by applying combination rules to the 10 completed‐data estimates.[17] We analyzed our primary and secondary predictors, adjusting for the confounders chosen a priori, clustered by facility with robust standard errors. An level of <0.05 was considered significant.

Sensitivity Analysis

We assumed that subjects missing a follow‐up status were ongoing smokers. However, given the high mortality rate observed in our cohort, we were concerned that some subjects lacking a follow‐up status may have died, missing the opportunity to have a quit attempt recorded. Therefore, we performed sensitivity analysis excluding subjects who died during the 6 to 12 months of follow‐up, repeating the imputation and analysis as described above. In addition, due to concern for indication bias in the choice of medication used for our secondary analysis, we performed propensity score matching for treatment with each medication in comparison to nicotine patch, using the teffects command, with 3 nearest neighbor matches. We included additional comorbidities in the propensity score matching.[18]

Association of Treatment With Study Medications and Quitting Smoking

In adjusted analyses, the odds of quitting smoking at 6 to 12 months were not greater among patients who were dispensed a study medication within 90 days of discharge (odds ratio [OR]: 0.88, 95% confidence interval [CI]: 0.74‐1.04). We found no association between counseling provided at discharge and smoking cessation (OR: 0.95, 95% CI: 0.0.66‐1.), adjusted for the receipt of medications. There was no difference in quit rate between patients dispensed medication within 48 hours of discharge, or between patients treated in the year prior to admission and again postdischarge (Table 2).

We then assessed differences in effectiveness between specific medications among the 450 patients who were dispensed medications. Using nicotine patch alone as the referent group, patients treated with varenicline demonstrated greater odds of smoking cessation (OR: 2.44, 95% CI: 1.48‐4.05). Patients treated with short‐acting NRT alone were less likely to report smoking cessation (OR: 0.66, 95% CI: 0.51‐0.85). Patients treated with buproprion or combination therapy were no more likely to report cessation (Table 3). When sensitivity analysis was performed using propensity score matching with additional variables included, there were no significant differences in the observed associations.

Our overall mortality rate observed at 1 year was 19.5%, nearly identical to previous cohort studies of patients admitted for COPD.[19, 20] Because of the possibility of behavioral differences on the part of patients and physicians regarding subjects with a limited life expectancy, we performed sensitivity analysis limited to the patients who survived to at least 12 months of follow‐up. One hundred six patients (7.9%) died during 6 to 12 months of follow‐up. There was no change in inference for our primary exposure (OR: 0.95, 95% CI: 0.79‐1.14) or any of the secondary exposures examined.

Study Cohort

We identified all smokers aged 40 years hospitalized between 2005 and 2012 with either a primary discharge diagnosis of COPD based on International Classification of Diseases, 9th Revision codes (491, 492, 493.2, and 496) or an admission diagnosis from the text of the admit notes indicating an exacerbation of COPD. We limited to patients aged 40 years to improve the specificity of the diagnosis of COPD, and we selected the first hospitalization that met inclusion criteria. We excluded subjects who died within 6 months of discharge (Figure 1).

Figure 1

To establish tobacco status, we built on previously developed and validated methodology,[11] and performed truncated natural language processing using phrases in the medical record that reflected patients' tobacco status, querying all notes from the day of admission up to 6 months prior. If no tobacco status was indicated in the notes, we identified the status encoded by the most recent health factor. We manually examined the results of the natural language processing and the determination of health factors to confirm the tobacco status. Manual review was undertaken by 1 of 2 trained study personnel. In the case of an ambiguous or contradictory status, an additional team member reviewed the information to attempt to make a determination. If no determination could be made, the record was coded to unknown. This method allowed us to identify a baseline status for all but 77 of the 3580 patients admitted for COPD.

Outcome and Exposure

The outcome was tobacco status at 6 to 12 months after discharge. Using the same methods developed for identification of baseline smoking status, we obtained smoking status for each subject up to 12 months postdischarge. If multiple notes and encounters were available indicating smoking status, we chose the latest within 12 months of discharge. Subjects lacking a follow‐up status were presumed to be smokers, a common assumption.[12] The 6 to 12month time horizon was chosen as these are the most common time points used to examine a sustained change in tobacco status,[13, 14, 15] and allowed for adequate time for treatment and clinical follow‐up.

Our primary exposure was any smoking cessation medication or combination dispensed within 90 days of discharge. This time horizon for treatment was chosen due to recent studies indicating this is a meaningful period for postdischarge treatment.[14] We assessed the use of nicotine patch, short‐acting nicotine, varenicline, buproprion, or any combination. Accurate data on the prescription and dispensing of these medications were available from the VA pharmacy record. Secondary exposure was the choice of medication dispensed among treated patients. We assessed additional exposures including receipt of cessation medications within 48 hours of discharge, treatment in the year prior to admission, and predischarge counseling. Predischarge counseling was determined as having occurred if nurses documented that they completed a discharge process focused on smoking cessation. Referral to a quit line is part of this process; however, due to the confidential nature of these interactions, generally low use of this service, and lack of linkage to the VA electronic health record, it was not considered in the analysis.

Confounders

Potential confounders were assessed in the year prior to admission up to discharge from the index hospitalization, with the use of mechanical or noninvasive ventilation assessed during the hospitalization. We adjusted for variables chosen a priori for their known or expected association with smoking cessation including demographics, Charlson Comorbidity Index,[16] markers of COPD severity (need for invasive or noninvasive mechanical ventilation during index hospitalization, use of oral steroids, long‐acting inhaled bronchodilators, and/or canister count of short‐acting bronchodilators in the year prior to admission), history of drug or alcohol abuse, homelessness, depression, psychosis, post‐traumatic stress disorder, lung cancer, coronary artery disease, and under‐ or overweight status. Nurse‐based counseling prior to discharge was included as a variable for adjustment for our primary and secondary predictors to assess the influence of pharmacotherapy specifically. Due to 3.1% missingness in body mass index, multiple imputation with chained equations was used to impute missing values, with 10 imputations performed. The imputation was performed using a linear regression model containing all variables included in the final model, grouped by facility.

Statistical Analysis

All analyses were performed using Stata 13 (StataCorp, College Station, TX) software. ² tests and t tests were used to assess for unadjusted bivariate associations. Using the pooled imputed datasets, we performed multivariable logistic regression to compare odds ratios for a change in smoking status, adjusting the estimates of coefficients and standard errors by applying combination rules to the 10 completed‐data estimates.[17] We analyzed our primary and secondary predictors, adjusting for the confounders chosen a priori, clustered by facility with robust standard errors. An level of <0.05 was considered significant.

Sensitivity Analysis

We assumed that subjects missing a follow‐up status were ongoing smokers. However, given the high mortality rate observed in our cohort, we were concerned that some subjects lacking a follow‐up status may have died, missing the opportunity to have a quit attempt recorded. Therefore, we performed sensitivity analysis excluding subjects who died during the 6 to 12 months of follow‐up, repeating the imputation and analysis as described above. In addition, due to concern for indication bias in the choice of medication used for our secondary analysis, we performed propensity score matching for treatment with each medication in comparison to nicotine patch, using the teffects command, with 3 nearest neighbor matches. We included additional comorbidities in the propensity score matching.[18]