Physician Staffing Patterns and Clinical Outcomes in Critically Ill Patients:  A Systematic Review FREE

Approximately 1% of the US gross domestic product is consumed in the care of intensive care unit (ICU) patients.¹ Despite this considerable investment of resources, there is wide variation in ICU organization,^2- 3 and studies have suggested that differences in ICU organization may affect patient outcome. For example, staffing ICUs with critical care physicians (intensivists) may improve clinical outcomes.⁴ A conceptual model that explains this finding is that physicians who have the skills to treat critically ill patients and who are immediately available to detect and treat problems may prevent or attenuate morbidity and mortality.² Staffing ICUs with intensivists may also decrease resource use because these physicians may be better at reducing inappropriate ICU admissions, preventing complications that prolong length of stay (LOS), and recognizing opportunities for prompt discharge.²

Intensive care unit staffing is typical of an organizational issue in health care in that, despite its potential importance in clinical and economic outcomes, it is not studied by using randomized trials. For example, the widely held belief that outcomes are better after surgery performed by experienced surgeons or hospitals is based solely on observational data.⁵ Practical and ethical reasons exist to explain why such organizational characteristics are not subjected to randomized trials. Yet, as changes occur in the way health care is organized, financed, and delivered, it will be important to understand the impact of organizational characteristics, such as ICU physician and nurse staffing, on patient outcomes through systematic reviews.⁶ To inform health policy, we will need to synthesize evidence that is predominantly observational. Accordingly, the goal of this systematic review was to examine the effect of ICU physician staffing on hospital and ICU mortality and LOS.

We sought to identify and review all studies that met the following criteria: randomized or observational controlled trials of critically ill adults or children, ICU physician staffing strategies, hospital and ICU mortality, and LOS.

To identify literature in electronic databases, we searched MEDLINE from January 1, 1965, through September 30, 2001, by using the following medical subject heading (MeSH) terms: intensive care units, ICU, health resources/utilization, hospitalization, medical staff, hospital organization and administration, personnel staffing and scheduling, length of stay, and LOS. We used the following text words: staffing, intensivist, critical, care, and specialist. We used the search strategy for retrieval of controlled clinical trials proposed by Robinson and Dickersin.⁷ To identify observational studies, we added the MeSH terms case-control study and retrospective study.

We also searched EMBASE, HealthStar (Health Services, Technology, Administration, and Research), and HSRPROJ (Health Services Research Projects in Progress) via Internet Grateful Med and The Cochrane Library (1998, issue 3), which contains the CENTRAL Database of Controlled Trials, the Database of Abstracts of Review Effectiveness, and the Cochrane Database of Systematic Reviews.

In addition, we used the related articles feature of PubMed, which identifies related articles by using a hierarchical search engine that is not solely based on MeSH headings. This search was completed with articles selected by 2 of the authors (P.J.P. and D.C.A.).^8- 12 Although we searched for non–English-language citations, subsequent article review involved only English-language publications. To identify studies published in abstract form only, we hand-searched the abstract proceedings from the annual scientific assemblies of the Society of Critical Care Medicine, the American College of Chest Physicians, and the American Thoracic Society from January 1, 1994, through December 31, 2001.

After all citations based on our search strategy were identified, 2 of the authors (P.J.P. and D.C.A.) independently reviewed each abstract to confirm eligibility. If an abstract was selected as eligible, the same authors independently reviewed the respective article, if available, to confirm that it met inclusion criteria. Abstracts from meeting proceedings were included if the data were not published as peer-reviewed articles. To resolve discrepancies, the 2 reviewers either had to reach consensus, or use a third reviewer (T.D.).

Using a data collection form, we extracted data from the studies to describe patient characteristics, study methods, and study findings. We also abstracted quantitative data regarding the intervention, cointerventions, study design and duration, unit of analysis, risk adjustment, degree of follow-up, adjustment of historical trends, and type of ICU. All data were abstracted independently by each of the 2 primary reviewers and verified for accuracy by the third reviewer, again with discussion used to resolve differences among reviewers. All reviewers were intensivists with formal training in clinical epidemiology and biostatistics. We did not mask the reviewers to author, institution, or journal because such masking reportedly makes little difference to the results of a systematic review.¹³

We measured the percentage of agreement before discussion among reviewers in study selection, study design, and data abstraction. For data synthesis, we constructed evidence tables to present data separately for the 4 main outcome variables: hospital mortality, ICU mortality, hospital LOS, and ICU LOS. Because of wide variation in the methods used to evaluate hospital costs, we did not include cost as an outcome.

We classified the study design as a randomized clinical trial, cohort study (prospective, retrospective, or historical control), case-control study, or outcomes study (cross-sectional). We classified the method of risk adjustment as follows: validated physiologic method (discrimination and calibration of the model previously reported), selected clinical data (discrimination and calibration of the model not reported), and no risk adjustment.

Because ICU physician staffing varied widely among studies in the control and intervention groups, we initially classified ICU physician staffing as follows: (1) closed ICU (the intensivist is the patient's primary attending physician), (2) mandatory critical care consultation (the intensivist is not the patient's primary attending physician, but every patient admitted to the ICU receives a critical care consultation), (3) elective critical care consultation (the intensivist is involved in the care of the patient only when the attending physician requests a consultation), and (4) no critical care physician (intensivists were unavailable). Because it is difficult to distinguish between a closed ICU and a mandatory critical care consultation, and because in several studies we were not able to do so, we further grouped ICU physician staffing into high intensity (mandatory intensivist consultation or closed ICU) or low intensity (no intensivist or elective intensivist consultation).

We elected to evaluate study quality as the risk of bias caused by temporal trends, confounding, and incomplete follow-up. We classified the risk of bias caused by temporal trends as low if the study duration was shorter than 2 years, medium if 2 through 4 years, and high if longer than 4 years. We classified the risk of bias from confounding as low if the authors used a validated physiologic method of risk adjustment, medium if the authors used selected clinical data, and high if the authors used no risk adjustment. We classified the risk of bias from incomplete follow-up as low if it was 90% to 100% complete; medium for 80% to 89% complete; and high for less than 80% complete.

Because the studies varied markedly in design, risk adjustment method, and ICU physician staffing in the control and intervention groups, we performed a qualitative and quantitative assessment of heterogeneity among trials. Because we considered the qualitative heterogeneity among studies to be significant, we were reluctant to perform a quantitative synthesis of study results.¹⁴ Nevertheless, we used the test for quantitative heterogeneity.^15- 16 We present a random-effects, summary relative risk (RR) by using the methods of DerSimonian.¹⁷ When the data were available, we summarized mortality data from each study with RRs, odds ratios (ORs), and estimated 95% confidence intervals (CIs) for the ORs by using Woolf's method.¹⁸ We summarized LOS data as a relative reduction. We evaluated for publication bias with a funnel plot. All statistical calculations were performed with STATA 7.0 statistical software (STATA Corp, College Station, Tex). When possible, we reported unadjusted and adjusted outcomes for baseline severity of illness. When absolute rates of hospital mortality were unavailable, we reported the observed-expected mortality rate, and when the SD of LOS data were unavailable, we assumed it to be equal to the mean.² We used mean rather than median LOS because few studies reported medians. Results were considered significant at P<.05.

We identified 3544 citations from the electronic search, of which 660 were duplicates and 294 were unavailable in English and were excluded. We also identified 13 citations from hand searching meeting proceedings. Of the 2590 abstracts reviewed, we rejected 2556 (99%) because the intervention was not ICU physician staffing or because the published abstract was superseded by the subsequent article. We rejected an additional 8 abstracts after reviewing and discussing the corresponding article because the intervention was not ICU physician staffing or because the reviewers were not able to determine the type of ICU physician staffing.^19- 26 Twenty-six studies^{2,8- 12,27- 46} met selection criteria (19 articles and 7 published abstracts). The reviewers had 99% crude agreement in the selection of eligible abstracts and 96% crude agreement in the selection of eligible articles (Table 1a). Figure 1⁴⁷ presents the study search strategy (QUOROM: Quality of Reporting of Meta-analyses).

Twenty studies (77%) were from North America,^{2,8,11- 12,27- 35,37- 42,46} 3 (12%) were from Europe,^9,44- 45 and 3 (12%) were from Asia.^10,36,43 Eleven (42%) were from academic medical centers,^{8- 10,12,28- 29,31,34,43,45- 46} 6 (23%) were from community teaching hospitals,^{11,27,32- 33,36,41} 4 (15%) were from nonteaching community hospitals,^30,35,38,44 and 5 (19%) included a variety of hospitals^{2,37,39- 40,42} (3 studies included all hospitals in Maryland^2,39- 40). One article included a prospective and retrospective control arm.¹¹ Because our goal was to describe the available literature, we treated this article as 2 studies and thus had 27 studies for qualitative synthesis (Table 1).

Table 1 summarizes important aspects of these 27 studies, which included ICU patients treated between 1979 and 2000. Study populations included medical patients in 11 studies (41%),^{11- 12,27- 28,32,36,38,42,44- 45} surgical patients in 9 (33%),^{2,10,29,31,33,39- 41,46} mixed medical and surgical patients in 4 (15%),^8- 9,30,35 and pediatric patients in 3 (11%).^34,37,43 Sample sizes varied from 177 to 5415 patients, with a mean sample size of 1001 patients (SD, 1190) and a median sample size of 551 patients (25%-75% interquartile range, 277-1213).

All of the studies used an observational design (Table 1). Twenty-two were cohort studies, with 19 using historical controls (before-and-after design),^{8- 12,28- 36,38,41,43- 45} 2 using concurrent controls,^11,46 and 1 using both.²⁷ Five studies were cross-sectional with concurrent controls.^{2,37,39- 40,42} In one study, the ICU physician staffing in the intervention group was via remote videoconferencing.⁴¹ Twenty of the studies evaluated a single ICU,^{8- 12,28- 36,38,41,43- 46} 2 evaluated 2 ICUs,^11,27 1 evaluated 16 ICUs,³⁷ 1 evaluated 35 ICUs,³⁹ 1 evaluated 39 ICUs,² 1 evaluated 42 ICUs,⁴² and 1 did not report the number of ICUs evaluated.⁴⁰

Twenty-five studies compared high with low-intensity ICU physician staffing. Of the remaining 2, one compared a closed ICU with a mandatory consultation²⁸ and the other compared elective consultation with no intensivist involved.³² Of the 25 studies comparing high with low-intensity staffing, 9 compared a closed ICU (intervention group) with elective consultation (control group),^{9,11,27,29,33,42- 44} 3 compared mandatory consultation (intervention) with no intensivist (control),^34,37,46 5 compared mandatory consultation (intervention) with elective consultation (control group),^2,38- 41 and 5 compared closed ICU (intervention) with no intensivist (control).^{8,30,35- 36,45} In 2 studies, we could not differentiate between a closed ICU and a mandatory consultation,^10,12 and in 2 studies^10,31 we could not differentiate between an elective consultation and no intensivist.

The quality characteristics of the studies are listed in Table 2. Fifteen of the 24 studies that reported the study period had low risk of bias from temporal trends, whereas 8 studies had medium risk and 1 had high risk. All 27 studies had complete follow-up and thus a low risk of bias from incomplete follow-up. No study followed up patients after hospital discharge.

Twenty-one of 27 studies had low risk of bias from confounding, whereas 6 studies had medium risk. All studies reported some form of risk adjustment. Twenty-one studies used a validated physiologic method (15 used the Acute Physiology and Chronic Health Evaluation Score [APACHE] only,^48- 49 2 used the Mortality Prediction Model,⁵⁰ 2 used the Pediatric Risk of Mortality Score,^51- 52 1 used the Physiologic Severity Index [PSI],⁵³ and 1 reported both APACHE II and the Glasgow Coma Scale⁵⁴). Six studies used selected clinical data (the first used nursing hours per patient,³⁵ a second used age, reason for admission, and mental status,³⁰ a third used a customized case-mix index and patient acuity measured by percentage of patients requiring mechanical ventilatory support,³⁸ and 3 others used discharge data in a regression model to adjust for patient demographics, severity of illness, comorbid disease, and hospital and surgeon volume^2,39- 40) (Table 1).

Eleven studies reported differences in severity of illness between the high- and low-intensity groups. In 4 studies,^{28,31,45- 46} the high-intensity group compared with the low-intensity group had significantly higher APACHE scores, suggesting higher baseline severity of illness. Three studies reported higher severity in the low-intensity group by using different severity instruments.^42- 44 Two studies reported higher baseline severity in the high-intensity group by using the distribution of the PSI score³⁴ and APACHE II score.¹⁰ Another study reported higher ICU nursing hours per day and suggested that this represented higher severity in the high-intensity physician staffing group.³⁵ The author of the study,³⁸ which used patient acuity and case-mix index, also suggested greater severity in the arm with the high-intensity physician staffing. There was no evidence of publication bias on a funnel plot of hospital mortality (Figure 2).

Hospital Mortality. Seventeen studies (63%) reported hospital mortality according to ICU physician staffing as a primary outcome measure (Table 3). The hospital mortality rate ranged from 6% to 74% in the low-intensity staffing group and from 1% to 57% in the high-intensity staffing group (Table 3). Overall, 16 (94%) of the 17 studies showed a decrease in hospital mortality rate for ICU patients with high-intensity physician staffing; in the one study that showed increased mortality with high-intensity physician staffing, the increase was not statistically significant.²⁸ In 10 (67%) of 15 studies^{2,8- 9,12,32,39- 42,44} that reported unadjusted mortality and 9 (64%) of 14 studies^{2,8,12,30,32,37,40- 41,44} that reported adjusted mortality, the decrease was statistically significant (Table 3). No study reported a statistically significant increase in hospital mortality with high-intensity ICU physician staffing. The random-effects pooled estimate of the unadjusted RR for high-intensity vs low-intensity staffing is 0.71 (95% CI, 0.62-0.82) (Figure 3A).

ICU Mortality. Fifteen studies (56%) evaluated the impact of ICU physician staffing on ICU mortality, with 12 studies (80%) reporting ICU mortality adjusted for severity of illness (Table 3). Overall, 14 (93%) of these 15 studies^{8- 10,27,29,31- 36,38,41,43} showed a decrease in ICU mortality rate for ICU patients with high-intensity physician staffing. Nine (69%) of the 13 studies^{8- 10,29,32,35,38,41,43} that reported unadjusted ICU mortality rates found a statistically significant reduction with high-intensity physician staffing in the ICU (Figure 3B and Table 3). In 9 (75%) of the 12 studies^{8- 10,29,32,34- 35,41,43} that adjusted for severity of illness, ICU mortality significantly decreased as well with high-intensity physician staffing. The random-effects, pooled estimate of the unadjusted RR for high-intensity vs low-intensity staffing is 0.61 (95% CI, 0.50-0.75).

Hospital LOS. Thirteen studies (48%) evaluated the impact of ICU physician staffing on hospital LOS (Table 4). The hospital LOS ranged from 8 to 33 days in the low-intensity group and 7 to 24 days in the high-intensity group. Ten (77%) of 13 studies reported a reduction in hospital LOS with high-intensity staffing (range of relative reduction, 5%-42%).^{2,11,28,32,36,39- 40,44,46} In 6 of these studies, the reduction was statistically significant (Figure 4A).^{2,11,32,39,46} Only 1 study (8%) reported a statistically significant increase in hospital LOS with high-intensity physician staffing, but this study compared patients admitted to a neurosurgical ICU with patients admitted to a general ICU, and the results were not adjusted for baseline severity of illness.⁴² Only 4 studies adjusted hospital LOS for baseline severity of illness.^2,39- 41 Two of these studies^2,39 showed a statistically significant decrease in hospital LOS with high-intensity physician staffing in the ICU, with the remaining 2 studies^40- 41 showing no significant difference in hospital LOS.³⁹

Intensive Care Unit LOS. Eighteen studies (67%) evaluated the impact of ICU physician staffing on ICU LOS (Table 4). The ICU LOS ranged from 2 to 13 days in the low-intensity group and 2 to 10 days in the high-intensity group. Fourteen (78%) of 18 studies reported that ICU LOS decreased with high-intensity physician staffing (Figure 4B).^{2,10- 11,29- 30,32- 33,36,38,41,43- 44,46} In 11 of these studies, this decrease was statistically significant.^{2,10- 11,32- 33,36,38,41,43,46} The study that compared a closed neurosurgical ICU to a general ICU was the only one to report a statistically significant increase in ICU LOS with high-intensity ICU physician staffing in the neurosurgical ICU.⁴² Three of 18 studies reported higher severity in the high-intensity group,^28,38,46 2 reported higher severity in the low-intensity group,^43- 44 and the remaining 13 reported no difference between the 2 groups.^{2,10- 12,29- 30,32- 34,36,41- 42} Only 2 studies adjusted ICU LOS for baseline severity of illness^2,42; ICU LOS in both studies favored high-intensity physician staffing.

We found that greater use of intensivists in the ICU led to significant reductions in ICU and hospital mortality and LOS. These findings were consistent across a variety of populations and hospital settings and have potentially important implications for patient care. Given the variation in ICU physician staffing and the potential for reduced mortality implied by these studies, a more rigorous evaluation of the optimal ICU organization is essential.

Intensive care is one of the largest and most expensive aspects of US health care. There are approximately 6000 ICUs in the United States,⁵⁵ caring for approximately 55 000 patients daily,⁵⁵ with an annual budget of approximately $180 billion.¹ The proportion of ICUs with high-intensity ICU physician staffing is unclear, but appears to be relatively small. In 1992, Groeger et al³ suggested that only 10% of ICUs in the United States require an intensivist to act as the patients' primary physician. In 1999, Schmitz et al⁵⁵ estimated that one third of all ICU patients in the United States were treated by intensivists acting as either primary physicians or consultants. Since most ICU patients are cared for with low-intensity physician staffing and high-intensity staffing appears to be associated with improved outcomes, mandatory ICU physician staffing may improve ICU process and outcomes.

The general lack of intensivist staffing in the United States contrasts with the usual closed ICU approach in Europe and Australia. A survey⁵⁶ by the Audit Commission for Local Authorities and the National Health Service in England and Wales found that closed systems are common and intensivists initiate care in 80% of all ICUs. The average 6-bed general ICU in the United Kingdom has 3 consultants with fixed commitments to the unit and 3 more taking part in the on-call rota.⁵⁶ According to Cole et al,⁵⁷ all ICUs in Victoria, the second most populous state in Australia, have been following the closed model for more than a decade. In 1997, a task force of the European Society of Intensive Care Medicine⁵⁸ issued recommendations on minimal requirements for intensive care departments (ICDs). Although the recommendations were not evidence based, the task force emphasized that the director of an ICD should be an intensivist and that it is essential that a qualified intensivist provide 24-hour coverage in level II and III (moderate- and high-intensity care) ICDs.⁵⁸ The task force also recommended 24-hour coverage by an intensivist for level I ICDs.⁵⁸

Our review identified several issues that may be important for researchers studying health care organizational characteristics. Our initial search, based on MeSH terms and text words, yielded a large number of citations, yet failed to identify several relevant articles that we had previously identified.^{8- 9,11- 12,28,30,32,34} Although each shared intensive care unit as a MeSH term, the assignment of other MeSH terms was inconsistent. By incorporating the related articles feature, we were able to identify additional relevant articles. The configuration of MeSH terms is not ideal for a comprehensive review of health care organizational characteristics, and investigators and library scientists should improve this indexing situation.

There are a number of potential limitations to consider regarding this literature. First, there is a risk of selection bias. Mark⁵⁹ describes 3 areas of possible selection bias in critical appraisal: selection of representative subjects (generalizability), selection of subjects to exposure (confounding variables), and selection of subjects at outcome (distorted samples). We believe the findings are generalizable because there was a consistent benefit associated with high-intensity staffing in studies of medical and surgical patients, studies from academic and community hospitals, and studies from inside and outside the United States. Because the studies are not randomized, the risk of confounding variables is considerable. However, an important strength of this literature was the consistent use of risk-adjustment methods. Critical care medicine has developed sophisticated, well-validated, risk-adjustment methods that use multiple clinical and physiologic variables to predict the risk of in-hospital death.^48- 52 In our analysis, 22 (81%) of 27 studies used such methods to minimize bias from confounding variables. Finally, all 27 studies had complete follow-up, and there was therefore no risk of bias from distorted samples.

A second potential limitation is publication bias. However, the funnel plot suggested that risk for publication bias was not significant (Figure 2). There was no quantitative heterogeneity among studies, and the results were consistent across studies, increasing our confidence in the validity of our conclusions. Moreover, from our discussions with staff of critical care societies (American Thoracic Society, American College of Chest Physicians, and Society of Critical Care Medicine at their annual meetings during 1999-2001), we found no evidence of any relevant negative unpublished studies.

A third potential limitation is risk for temporal trends in mortality to bias study results. Temporal trends in any before-and-after study design could affect the results of this review and reduce the strength of our inferences. We believe this source of bias is small for several reasons. First, evidence for the effectiveness of therapies in reducing mortality in critically ill patients occurred only at the end of the study periods.^60- 62 Second, there were no trends for reduced mortality in critically ill patients during the study periods. Third, most of the studies were conducted during a short period, and thus the effect of any temporal trends is likely small.

A fourth potential limitation is the use of ICU mortality and LOS as outcome measures. Because no study described explicit criteria for discharge from the ICU, differences in discharge practices between the treatment and control groups may have influenced the results. For example, early ICU discharge may have artificially reduced ICU mortality without decreasing hospital mortality. However, the improvement in mortality and LOS observed with high-intensity ICU physician staffing was observed at ICU and hospital discharge.

There are also limitations in the way we conducted our review. First, 3 of the authors (P.J.P., D.C.A., and T.D.) are intensivists and potentially biased. The high degree of agreement among reviewers may be due to similar clinical and research interests and may have encoded systematic error. Second, we included only articles published in English, although we are not aware of relevant non–English-language publications. The exclusion of non–English-language articles should not significantly affect the study results.⁶³ Third, we did not perform a formal evaluation of study quality, because the particular scale chosen may influence the results.⁶⁴ Rather, we identified relevant methodologic aspects of the study (a priori) and assessed these individually.

Our systematic review was rigorously conducted and transparently reported, following recommendations outlined by the Meta-analysis of Observational Studies in Epidemiology Group.¹⁴ Because it is unclear how to proceed when there is qualitative but not quantitative heterogeneity among studies, we present pooled estimates by using the random-effects model and recommend cautious interpretation of these results.

We should attempt to identify the characteristics of high-intensity ICU staffing that improved outcome. We found previously that daily rounds by an ICU physician were associated with improved outcomes in patients who underwent abdominal aortic surgery. Yet how daily rounds translate into improved outcomes remains unclear.² For example, were the improved outcomes due to specific critical care training and expertise or to increased availability, perhaps with reduced response time, of a team of physicians whose sole responsibility was to provide care in the ICU? Some of the improvements may be possible through alternative staffing models, such as telemedicine.⁴¹ Finally, other ICU characteristics, such as nurse-to-patient ratios, also affect patient outcomes.⁶⁵ Determining how to best organize ICU staffing from a multidisciplinary standpoint to optimize patient outcomes is a high research priority. Meanwhile, our findings provide evidence to support the recommendations by the Leapfrog Group^66- 67 and Society of Critical Medicine for ICU physician staffing.⁶⁸ We believe this systematic review summarizes and clarifies the available literature, helps guide public policy, and provides a basis for future research.