Original Research

The Philadelphia Panel evidence-based clinical guidelines on musculoskeletal rehabilitation interventions were published as 5 separate articles in the October 2001 issue of Physical Therapy, the journal of the American Physical Therapy Association.^1-5 Originally convened on December 17, 1999, the panel included member representatives from the American Physical Therapy Association (Andrew A. Guccione, PT, PhD), the American College of Rheumatology (Scott M. Hasson, PT, PhD), the American Academy of Orthopedic Surgeons (John Albright, MD), the American Academy of Neurology (Bruce Dobkin, MD), the American College of Physicians (Richard Allman, MD, and Alicia Conill, MD), the Cochrane Back Group (Paul Shekelle, PhD), the American Society of Physical Medicine and Rehabilitation (Randolph Russo, MD, and Richard Paul Bonfiglio, MD), and the American Academy of Family Physicians (Jeffrey L. Susman, MD). The purpose of the group was to create evidence-based practice guidelines that identify the clinical benefit of rehabilitation interventions for low back, knee, neck, and shoulder problems. The guidelines did not address medical or pharmacologic management of these conditions. Although the guidelines primarily benefit the rehabilitation specialist (physical therapists, occupational therapists, and sports therapists), family practitioners and other primary care physicians are responsible for managing these conditions and their treatments. By knowing which rehabilitation interventions have proven clinical benefit, physicians can better coordinate a patient’s care and make evidence-based decisions when ordering physical therapy. In this report, we summarize and disseminate these guidelines for specific rehabilitation modalities in the management of common conditions that cause back pain, knee pain, neck pain, or shoulder pain.

Background

The Philadelphia Panel is not a novel evaluation of evidence-based rehabilitation interventions. Previous assessments of therapies have been published by Disorders; the Agency for Health Care Policy and Research (guidelines for low back problems); the British Medical Journal; Clinical Evidence; and the American College of Rheumatology (guidelines for knee osteoarthritis). However, those guidelines had significant limitations or have become outdated. The Philadelphia Panel set out to provide a structured and rigorous set of evidence-based clinical guidelines for the conservative (nonsurgical) management of conditions associated with low back, knee, neck, or shoulder pain.

Professional organizations of clinicians who routinely care for patients with back, knee, neck, and shoulder pain nominated members to create the Philadelphia Panel. Panelists were nominated based on their clinical expertise and previous experience developing evidence-based guidelines. Members of the panel included an orthopedic surgeon, a rheumatologist, an internist, a physiatrist, a neurologist, a family physician, a doctorate-level researcher from the Cochrane Back Group, and 2 physical therapists. The panel chair formed a research staff to identify and screen articles and construct evidence tables for pertinent references.

Development of guidelines

To provide evidence-based practice guidelines for each condition, a 5-step process was established: defining the intervention, collecting the evidence, synthesizing the results, making recommendations based on the research, and grading the strength of the recommendations. To prepare the data, systematic reviews were performed for the conditions of interest and specific interventions. Rehabilitation interventions frequently used in the care of low back, knee, neck, and shoulder pain were identified, and the patient population was defined. Therapeutic exercise, massage, transcutaneous electrical nerve stimulation (TENS), thermotherapy, ultrasound, electrical stimulation, and combinations of these therapies were included in the literature search. Evidence from randomized controlled trials and observational studies such as controlled clinical trials, cohort studies, and case-control studies was identified and analyzed. Studies were included if they had evaluated outcome measures such as pain, function, strength, range of motion, return to work, patient satisfaction, activities of daily living, or quality of life. Data from studies that included outpatient adults with vertebral disk disease, scoliosis, cancer, or pulmonary, neurologic, cardiac, dermatologic, or psychiatric conditions were excluded.

The data from pertinent articles were synthesized, and the relative clinical benefit between treatment and control groups was calculated for each condition for each intervention. The panel deemed a 15% or greater improvement between treatment and control groups to be clinically important. Relevant studies were then graded according to the type and clinical importance of the presented data. The grading scheme is summarized in Table 1. Once the panel compiled the intervention recommendations for each condition, external review by practitioners ensured the relevance of the recommendations. Interventions with a grade of A or B were to be included in the guidelines. No grade B recommendations were made. Grade C interventions could be neither included nor excluded in the final guidelines due to lack of demonstrated clinical benefit.

TABLE 1
Details of the Philadelphia Panel Classification System*

Recommendations for low back pain

Low back pain results in significant socioeconomic repercussions due to the restriction of occupational activities and functional ability in the activities of daily living. Treatment goals in the care of patients with low back pain include relief from pain, reduction of muscle spasm, improvement in range of motion and strength, correction of postural problems, and improvement of functional status at work and in daily life. The care of patients with low back pain can be a very frustrating process for physicians or therapists. Use of treatment modalities with proven effectiveness can provide structure and credibility to the recovery process. The Philadelphia Panel’s recommendations are summarized in Table 2.

The panel found grade A evidence for improvement in the ability to return to work with continuation of normal activity vs enforced bedrest for acute low back pain (<4 weeks). Interestingly, no clinically important benefit was shown for the continuation of normal activity for the improvement, of pain (5% decrease) or function (10% improvement). It is important to note that the recommendations for low back pain are based on studies that excluded patients with disk involvement; therefore, the effects of continuing normal activity in patients with acute back pain and disk involvement were not assessed. The Philadelphia Panel chose not to evaluate data from studies with vertebral disk involvement in their patient population.

With regard to acute low back pain, data from randomized controlled trials demonstrated no clinically important benefit (<15% from control) of stretching or strengthening exercises, mechanical traction, or TENS. Likewise, a study of therapeutic ultrasound showed no demonstrable clinical benefit. There was poor evidence to include or exclude these modalities alone as an intervention for acute low back pain. No study with an acceptable research design was identified for thermotherapy, electrical stimulation, therapeutic massage, or electromyographic biofeedback as interventions for low back pain.

For subacute low back pain (4–12 weeks), data from randomized controlled trials showed a clinically significant improvement in pain, function, and global assessment from therapeutic exercise. Mechanical traction for subacute low back pain was given a grade C rating for patient global improvement and return to work. Consequently, there is poor evidence to include or exclude mechanical traction alone for low back pain.

The assessment of chronic low back pain (>12 weeks) identified 1 grade A guideline. Therapeutic exercise, including stretching, strengthening, and mobility exercises, resulted in clinically significant improvement in pain and function but had no clinical benefit in facilitating return to work. Mechanical traction, TENS, electromyographic biofeedback, and therapeutic ultrasound showed no clinical benefit. No studies assessed efficacy of thermotherapy, massage, or electrical stimulation.

Back pain due to prior back surgery was considered separately from other conditions. A grade A guideline was given to therapeutic exercise for pain due to prior back surgery.

Combinations of rehabilitation interventions for acute and chronic low back pain produced insufficient data to make a recommendation. Although most patients who are referred to physical therapy undergo combination therapy, the panel could not formalize a guideline for combination therapy.

TABLE 2
Summary grid of low back pain guidelines*

Recommendations for knee pain

Chronic knee pain is one of the more common complaints presented to primary care physicians. Acute and chronic pain can be related to acute injury, osteoarthritis, overuse injuries, or knee surgery. Due to the frequency of knee pain and its tendency to improve with time, there is a need to provide clinicians with the ability to make informed decisions regarding treatment options. The panel’s recommendations are summarized in Table 3.

The Philadelphia Panel identified two interventions that demonstrated grade A data for the treatment of osteoarthritis. Therapeutic exercise and TENS showed clinically important benefit for pain and patient global assessment in osteoarthritis. Thermotherapy, ultrasound, and electrical stimulation demonstrated no clinically important benefit for knee osteoarthritis. In summary, there is poor evidence to include or exclude thermotherapy, ultrasound, or electrical stimulation in the treatment of knee osteoarthritis.

With regard to knee tendonitis, the only intervention with significant data was deep transverse friction massage, which showed no clinical benefit. Patellofemoral pain also had 1 grade C intervention recommendation for the use of ultrasound. Further, preoperative exercise, thermotherapy, and TENS showed no clinical benefit for the management of postsurgical knee pain.

The remaining interventions for osteoarthritis of the knee, patellofemoral pain, tendonitis of the knee, and postsurgical pain showed insufficient evidence for the Philadelphia Panel to make guideline recommendations. The major implication of this analysis is that there is poor evidence to support the use of several widely accepted interventions in the treatment of knee pain.

TABLE 3
Summary grid of knee pain guidelines*

Recommendations for neck pain

Acute neck pain is often associated with injury or accident, whereas chronic neck pain is related to repetitive injury. Neck pain is commonly managed with analgesics and rest, but referrals to rehabilitation are increasing. The Philadelphia Panel sought to improve the appropriate use of rehabilitation interventions for neck pain by providing evidence-based guidelines. A summary of the Panel’s recommendations can be found in Table 4.

Only 8 trials met all selection criteria for the management of neck pain. Of these trials, only proprioceptive and therapeutic exercise for chronic neck pain showed clinical benefit for pain and function. The remaining studies showed no clinical benefit or insufficient data. Mechanical traction showed no clinically important benefit in the treatment of acute or chronic neck pain. No further studies that met selection criteria were found with regard to rehabilitation interventions for neck pain. Clearly there are insufficient data in the medical literature with regard to neck pain.

TABLE 4
Summary grid of neck pain guidelines*

Recommendations for shoulder pain

Rehabilitation specialists offer several conservative interventions for the management of shoulder pain. There are few published guidelines for the management of shoulder pain. Results of the analysis are shown in Table 5. As in the analysis of neck pain, the Philadelphia Panel was able to develop a single recommendation with clinical benefit. Clinically important benefit was shown for ultrasound for calcific tendonitis. There was no evidence of clinically important benefit for the use of ultrasound for capsulitis, bursitis, or tendonitis.

TABLE 5
Summary grid of shoulder pain guidelines*

Discussion

By using a rigorous methodology, the Philadelphia Panel has created evidence-based clinical practice guidelines for low back, knee, neck, and shoulder pain rehabilitation based on the current medical literature. Despite the thorough techniques used to create the guidelines, there are methodologic limitations, as with all such reviews. The panel identified many problems with the current body of evidence in the medical literature. The main difficulty with the current literature is the lack of standardization of outcome measurements used in different studies. Future studies need to develop standards of measurement that are valid, reliable, and sensitive to changes in outcome. Further, current studies have used broad inclusion criteria and enrolled patients with diverse etiologies for their pain. Problems with selection and description of patients, definitions of conditions, and standardizations of treatments and outcome measures need to be solved to properly demonstrate benefit from a rehabilitation intervention and remove misclassification bias.

Another limitation is the inherent difficulty of studying rehabilitation interventions. The effectiveness of physical rehabilitation interventions is affected by psychosocial, physical, and occupational factors. These factors can be minimized by fully randomizing large patient groups, thus minimizing selection bias. Another difficulty with developing high-quality randomized controlled trials in the area of rehabilitation is the blinding of patients or caregivers to interventions.

In future studies, it will be necessary to specifically clarify the type and manner of an intervention, intervention intensity and duration, and progression of the intervention according to patient-specific outcomes. Further, a patient typically receives several rehabilitation interventions during a therapy session. These modalities change depending on the phase of recovery (ie, ice, rest, and compression initially, evolving to strengthening, stretching, and electrotherapy with progress). A more thorough means of standardizing this progression in a patient’s care is needed.

In addition, the guidelines did not address cost, patient preferences, or potential harm associated with each intervention for the specific conditions.

Overall, there is a pressing need for further work in the study of rehabilitation interventions, due especially to the increased use of physical therapy for the management of low back pain, knee pain, neck pain, and shoulder pain.

The Philadelphia Panel evidence-based clinical guidelines on musculoskeletal rehabilitation interventions were published as 5 separate articles in the October 2001 issue of Physical Therapy, the journal of the American Physical Therapy Association.^1-5 Originally convened on December 17, 1999, the panel included member representatives from the American Physical Therapy Association (Andrew A. Guccione, PT, PhD), the American College of Rheumatology (Scott M. Hasson, PT, PhD), the American Academy of Orthopedic Surgeons (John Albright, MD), the American Academy of Neurology (Bruce Dobkin, MD), the American College of Physicians (Richard Allman, MD, and Alicia Conill, MD), the Cochrane Back Group (Paul Shekelle, PhD), the American Society of Physical Medicine and Rehabilitation (Randolph Russo, MD, and Richard Paul Bonfiglio, MD), and the American Academy of Family Physicians (Jeffrey L. Susman, MD). The purpose of the group was to create evidence-based practice guidelines that identify the clinical benefit of rehabilitation interventions for low back, knee, neck, and shoulder problems. The guidelines did not address medical or pharmacologic management of these conditions. Although the guidelines primarily benefit the rehabilitation specialist (physical therapists, occupational therapists, and sports therapists), family practitioners and other primary care physicians are responsible for managing these conditions and their treatments. By knowing which rehabilitation interventions have proven clinical benefit, physicians can better coordinate a patient’s care and make evidence-based decisions when ordering physical therapy. In this report, we summarize and disseminate these guidelines for specific rehabilitation modalities in the management of common conditions that cause back pain, knee pain, neck pain, or shoulder pain.

Background

The Philadelphia Panel is not a novel evaluation of evidence-based rehabilitation interventions. Previous assessments of therapies have been published by Disorders; the Agency for Health Care Policy and Research (guidelines for low back problems); the British Medical Journal; Clinical Evidence; and the American College of Rheumatology (guidelines for knee osteoarthritis). However, those guidelines had significant limitations or have become outdated. The Philadelphia Panel set out to provide a structured and rigorous set of evidence-based clinical guidelines for the conservative (nonsurgical) management of conditions associated with low back, knee, neck, or shoulder pain.

Professional organizations of clinicians who routinely care for patients with back, knee, neck, and shoulder pain nominated members to create the Philadelphia Panel. Panelists were nominated based on their clinical expertise and previous experience developing evidence-based guidelines. Members of the panel included an orthopedic surgeon, a rheumatologist, an internist, a physiatrist, a neurologist, a family physician, a doctorate-level researcher from the Cochrane Back Group, and 2 physical therapists. The panel chair formed a research staff to identify and screen articles and construct evidence tables for pertinent references.

Development of guidelines

To provide evidence-based practice guidelines for each condition, a 5-step process was established: defining the intervention, collecting the evidence, synthesizing the results, making recommendations based on the research, and grading the strength of the recommendations. To prepare the data, systematic reviews were performed for the conditions of interest and specific interventions. Rehabilitation interventions frequently used in the care of low back, knee, neck, and shoulder pain were identified, and the patient population was defined. Therapeutic exercise, massage, transcutaneous electrical nerve stimulation (TENS), thermotherapy, ultrasound, electrical stimulation, and combinations of these therapies were included in the literature search. Evidence from randomized controlled trials and observational studies such as controlled clinical trials, cohort studies, and case-control studies was identified and analyzed. Studies were included if they had evaluated outcome measures such as pain, function, strength, range of motion, return to work, patient satisfaction, activities of daily living, or quality of life. Data from studies that included outpatient adults with vertebral disk disease, scoliosis, cancer, or pulmonary, neurologic, cardiac, dermatologic, or psychiatric conditions were excluded.

The data from pertinent articles were synthesized, and the relative clinical benefit between treatment and control groups was calculated for each condition for each intervention. The panel deemed a 15% or greater improvement between treatment and control groups to be clinically important. Relevant studies were then graded according to the type and clinical importance of the presented data. The grading scheme is summarized in Table 1. Once the panel compiled the intervention recommendations for each condition, external review by practitioners ensured the relevance of the recommendations. Interventions with a grade of A or B were to be included in the guidelines. No grade B recommendations were made. Grade C interventions could be neither included nor excluded in the final guidelines due to lack of demonstrated clinical benefit.

TABLE 1
Details of the Philadelphia Panel Classification System*

Recommendations for low back pain

Low back pain results in significant socioeconomic repercussions due to the restriction of occupational activities and functional ability in the activities of daily living. Treatment goals in the care of patients with low back pain include relief from pain, reduction of muscle spasm, improvement in range of motion and strength, correction of postural problems, and improvement of functional status at work and in daily life. The care of patients with low back pain can be a very frustrating process for physicians or therapists. Use of treatment modalities with proven effectiveness can provide structure and credibility to the recovery process. The Philadelphia Panel’s recommendations are summarized in Table 2.

The panel found grade A evidence for improvement in the ability to return to work with continuation of normal activity vs enforced bedrest for acute low back pain (<4 weeks). Interestingly, no clinically important benefit was shown for the continuation of normal activity for the improvement, of pain (5% decrease) or function (10% improvement). It is important to note that the recommendations for low back pain are based on studies that excluded patients with disk involvement; therefore, the effects of continuing normal activity in patients with acute back pain and disk involvement were not assessed. The Philadelphia Panel chose not to evaluate data from studies with vertebral disk involvement in their patient population.

With regard to acute low back pain, data from randomized controlled trials demonstrated no clinically important benefit (<15% from control) of stretching or strengthening exercises, mechanical traction, or TENS. Likewise, a study of therapeutic ultrasound showed no demonstrable clinical benefit. There was poor evidence to include or exclude these modalities alone as an intervention for acute low back pain. No study with an acceptable research design was identified for thermotherapy, electrical stimulation, therapeutic massage, or electromyographic biofeedback as interventions for low back pain.

For subacute low back pain (4–12 weeks), data from randomized controlled trials showed a clinically significant improvement in pain, function, and global assessment from therapeutic exercise. Mechanical traction for subacute low back pain was given a grade C rating for patient global improvement and return to work. Consequently, there is poor evidence to include or exclude mechanical traction alone for low back pain.

The assessment of chronic low back pain (>12 weeks) identified 1 grade A guideline. Therapeutic exercise, including stretching, strengthening, and mobility exercises, resulted in clinically significant improvement in pain and function but had no clinical benefit in facilitating return to work. Mechanical traction, TENS, electromyographic biofeedback, and therapeutic ultrasound showed no clinical benefit. No studies assessed efficacy of thermotherapy, massage, or electrical stimulation.

Back pain due to prior back surgery was considered separately from other conditions. A grade A guideline was given to therapeutic exercise for pain due to prior back surgery.

Combinations of rehabilitation interventions for acute and chronic low back pain produced insufficient data to make a recommendation. Although most patients who are referred to physical therapy undergo combination therapy, the panel could not formalize a guideline for combination therapy.

TABLE 2
Summary grid of low back pain guidelines*

Recommendations for knee pain

Chronic knee pain is one of the more common complaints presented to primary care physicians. Acute and chronic pain can be related to acute injury, osteoarthritis, overuse injuries, or knee surgery. Due to the frequency of knee pain and its tendency to improve with time, there is a need to provide clinicians with the ability to make informed decisions regarding treatment options. The panel’s recommendations are summarized in Table 3.

The Philadelphia Panel identified two interventions that demonstrated grade A data for the treatment of osteoarthritis. Therapeutic exercise and TENS showed clinically important benefit for pain and patient global assessment in osteoarthritis. Thermotherapy, ultrasound, and electrical stimulation demonstrated no clinically important benefit for knee osteoarthritis. In summary, there is poor evidence to include or exclude thermotherapy, ultrasound, or electrical stimulation in the treatment of knee osteoarthritis.

With regard to knee tendonitis, the only intervention with significant data was deep transverse friction massage, which showed no clinical benefit. Patellofemoral pain also had 1 grade C intervention recommendation for the use of ultrasound. Further, preoperative exercise, thermotherapy, and TENS showed no clinical benefit for the management of postsurgical knee pain.

The remaining interventions for osteoarthritis of the knee, patellofemoral pain, tendonitis of the knee, and postsurgical pain showed insufficient evidence for the Philadelphia Panel to make guideline recommendations. The major implication of this analysis is that there is poor evidence to support the use of several widely accepted interventions in the treatment of knee pain.

TABLE 3
Summary grid of knee pain guidelines*

Recommendations for neck pain

Acute neck pain is often associated with injury or accident, whereas chronic neck pain is related to repetitive injury. Neck pain is commonly managed with analgesics and rest, but referrals to rehabilitation are increasing. The Philadelphia Panel sought to improve the appropriate use of rehabilitation interventions for neck pain by providing evidence-based guidelines. A summary of the Panel’s recommendations can be found in Table 4.

Only 8 trials met all selection criteria for the management of neck pain. Of these trials, only proprioceptive and therapeutic exercise for chronic neck pain showed clinical benefit for pain and function. The remaining studies showed no clinical benefit or insufficient data. Mechanical traction showed no clinically important benefit in the treatment of acute or chronic neck pain. No further studies that met selection criteria were found with regard to rehabilitation interventions for neck pain. Clearly there are insufficient data in the medical literature with regard to neck pain.

TABLE 4
Summary grid of neck pain guidelines*

Recommendations for shoulder pain

Rehabilitation specialists offer several conservative interventions for the management of shoulder pain. There are few published guidelines for the management of shoulder pain. Results of the analysis are shown in Table 5. As in the analysis of neck pain, the Philadelphia Panel was able to develop a single recommendation with clinical benefit. Clinically important benefit was shown for ultrasound for calcific tendonitis. There was no evidence of clinically important benefit for the use of ultrasound for capsulitis, bursitis, or tendonitis.

TABLE 5
Summary grid of shoulder pain guidelines*

Discussion

By using a rigorous methodology, the Philadelphia Panel has created evidence-based clinical practice guidelines for low back, knee, neck, and shoulder pain rehabilitation based on the current medical literature. Despite the thorough techniques used to create the guidelines, there are methodologic limitations, as with all such reviews. The panel identified many problems with the current body of evidence in the medical literature. The main difficulty with the current literature is the lack of standardization of outcome measurements used in different studies. Future studies need to develop standards of measurement that are valid, reliable, and sensitive to changes in outcome. Further, current studies have used broad inclusion criteria and enrolled patients with diverse etiologies for their pain. Problems with selection and description of patients, definitions of conditions, and standardizations of treatments and outcome measures need to be solved to properly demonstrate benefit from a rehabilitation intervention and remove misclassification bias.

Another limitation is the inherent difficulty of studying rehabilitation interventions. The effectiveness of physical rehabilitation interventions is affected by psychosocial, physical, and occupational factors. These factors can be minimized by fully randomizing large patient groups, thus minimizing selection bias. Another difficulty with developing high-quality randomized controlled trials in the area of rehabilitation is the blinding of patients or caregivers to interventions.

In future studies, it will be necessary to specifically clarify the type and manner of an intervention, intervention intensity and duration, and progression of the intervention according to patient-specific outcomes. Further, a patient typically receives several rehabilitation interventions during a therapy session. These modalities change depending on the phase of recovery (ie, ice, rest, and compression initially, evolving to strengthening, stretching, and electrotherapy with progress). A more thorough means of standardizing this progression in a patient’s care is needed.

In addition, the guidelines did not address cost, patient preferences, or potential harm associated with each intervention for the specific conditions.

Overall, there is a pressing need for further work in the study of rehabilitation interventions, due especially to the increased use of physical therapy for the management of low back pain, knee pain, neck pain, and shoulder pain.

The Philadelphia Panel evidence-based clinical guidelines on musculoskeletal rehabilitation interventions were published as 5 separate articles in the October 2001 issue of Physical Therapy, the journal of the American Physical Therapy Association.^1-5 Originally convened on December 17, 1999, the panel included member representatives from the American Physical Therapy Association (Andrew A. Guccione, PT, PhD), the American College of Rheumatology (Scott M. Hasson, PT, PhD), the American Academy of Orthopedic Surgeons (John Albright, MD), the American Academy of Neurology (Bruce Dobkin, MD), the American College of Physicians (Richard Allman, MD, and Alicia Conill, MD), the Cochrane Back Group (Paul Shekelle, PhD), the American Society of Physical Medicine and Rehabilitation (Randolph Russo, MD, and Richard Paul Bonfiglio, MD), and the American Academy of Family Physicians (Jeffrey L. Susman, MD). The purpose of the group was to create evidence-based practice guidelines that identify the clinical benefit of rehabilitation interventions for low back, knee, neck, and shoulder problems. The guidelines did not address medical or pharmacologic management of these conditions. Although the guidelines primarily benefit the rehabilitation specialist (physical therapists, occupational therapists, and sports therapists), family practitioners and other primary care physicians are responsible for managing these conditions and their treatments. By knowing which rehabilitation interventions have proven clinical benefit, physicians can better coordinate a patient’s care and make evidence-based decisions when ordering physical therapy. In this report, we summarize and disseminate these guidelines for specific rehabilitation modalities in the management of common conditions that cause back pain, knee pain, neck pain, or shoulder pain.

Background

The Philadelphia Panel is not a novel evaluation of evidence-based rehabilitation interventions. Previous assessments of therapies have been published by Disorders; the Agency for Health Care Policy and Research (guidelines for low back problems); the British Medical Journal; Clinical Evidence; and the American College of Rheumatology (guidelines for knee osteoarthritis). However, those guidelines had significant limitations or have become outdated. The Philadelphia Panel set out to provide a structured and rigorous set of evidence-based clinical guidelines for the conservative (nonsurgical) management of conditions associated with low back, knee, neck, or shoulder pain.

Professional organizations of clinicians who routinely care for patients with back, knee, neck, and shoulder pain nominated members to create the Philadelphia Panel. Panelists were nominated based on their clinical expertise and previous experience developing evidence-based guidelines. Members of the panel included an orthopedic surgeon, a rheumatologist, an internist, a physiatrist, a neurologist, a family physician, a doctorate-level researcher from the Cochrane Back Group, and 2 physical therapists. The panel chair formed a research staff to identify and screen articles and construct evidence tables for pertinent references.

Development of guidelines

To provide evidence-based practice guidelines for each condition, a 5-step process was established: defining the intervention, collecting the evidence, synthesizing the results, making recommendations based on the research, and grading the strength of the recommendations. To prepare the data, systematic reviews were performed for the conditions of interest and specific interventions. Rehabilitation interventions frequently used in the care of low back, knee, neck, and shoulder pain were identified, and the patient population was defined. Therapeutic exercise, massage, transcutaneous electrical nerve stimulation (TENS), thermotherapy, ultrasound, electrical stimulation, and combinations of these therapies were included in the literature search. Evidence from randomized controlled trials and observational studies such as controlled clinical trials, cohort studies, and case-control studies was identified and analyzed. Studies were included if they had evaluated outcome measures such as pain, function, strength, range of motion, return to work, patient satisfaction, activities of daily living, or quality of life. Data from studies that included outpatient adults with vertebral disk disease, scoliosis, cancer, or pulmonary, neurologic, cardiac, dermatologic, or psychiatric conditions were excluded.

The data from pertinent articles were synthesized, and the relative clinical benefit between treatment and control groups was calculated for each condition for each intervention. The panel deemed a 15% or greater improvement between treatment and control groups to be clinically important. Relevant studies were then graded according to the type and clinical importance of the presented data. The grading scheme is summarized in Table 1. Once the panel compiled the intervention recommendations for each condition, external review by practitioners ensured the relevance of the recommendations. Interventions with a grade of A or B were to be included in the guidelines. No grade B recommendations were made. Grade C interventions could be neither included nor excluded in the final guidelines due to lack of demonstrated clinical benefit.

TABLE 1
Details of the Philadelphia Panel Classification System*

Recommendations for low back pain

Low back pain results in significant socioeconomic repercussions due to the restriction of occupational activities and functional ability in the activities of daily living. Treatment goals in the care of patients with low back pain include relief from pain, reduction of muscle spasm, improvement in range of motion and strength, correction of postural problems, and improvement of functional status at work and in daily life. The care of patients with low back pain can be a very frustrating process for physicians or therapists. Use of treatment modalities with proven effectiveness can provide structure and credibility to the recovery process. The Philadelphia Panel’s recommendations are summarized in Table 2.

The panel found grade A evidence for improvement in the ability to return to work with continuation of normal activity vs enforced bedrest for acute low back pain (<4 weeks). Interestingly, no clinically important benefit was shown for the continuation of normal activity for the improvement, of pain (5% decrease) or function (10% improvement). It is important to note that the recommendations for low back pain are based on studies that excluded patients with disk involvement; therefore, the effects of continuing normal activity in patients with acute back pain and disk involvement were not assessed. The Philadelphia Panel chose not to evaluate data from studies with vertebral disk involvement in their patient population.

With regard to acute low back pain, data from randomized controlled trials demonstrated no clinically important benefit (<15% from control) of stretching or strengthening exercises, mechanical traction, or TENS. Likewise, a study of therapeutic ultrasound showed no demonstrable clinical benefit. There was poor evidence to include or exclude these modalities alone as an intervention for acute low back pain. No study with an acceptable research design was identified for thermotherapy, electrical stimulation, therapeutic massage, or electromyographic biofeedback as interventions for low back pain.

For subacute low back pain (4–12 weeks), data from randomized controlled trials showed a clinically significant improvement in pain, function, and global assessment from therapeutic exercise. Mechanical traction for subacute low back pain was given a grade C rating for patient global improvement and return to work. Consequently, there is poor evidence to include or exclude mechanical traction alone for low back pain.

The assessment of chronic low back pain (>12 weeks) identified 1 grade A guideline. Therapeutic exercise, including stretching, strengthening, and mobility exercises, resulted in clinically significant improvement in pain and function but had no clinical benefit in facilitating return to work. Mechanical traction, TENS, electromyographic biofeedback, and therapeutic ultrasound showed no clinical benefit. No studies assessed efficacy of thermotherapy, massage, or electrical stimulation.

Back pain due to prior back surgery was considered separately from other conditions. A grade A guideline was given to therapeutic exercise for pain due to prior back surgery.

Combinations of rehabilitation interventions for acute and chronic low back pain produced insufficient data to make a recommendation. Although most patients who are referred to physical therapy undergo combination therapy, the panel could not formalize a guideline for combination therapy.

TABLE 2
Summary grid of low back pain guidelines*

Recommendations for knee pain

Chronic knee pain is one of the more common complaints presented to primary care physicians. Acute and chronic pain can be related to acute injury, osteoarthritis, overuse injuries, or knee surgery. Due to the frequency of knee pain and its tendency to improve with time, there is a need to provide clinicians with the ability to make informed decisions regarding treatment options. The panel’s recommendations are summarized in Table 3.

The Philadelphia Panel identified two interventions that demonstrated grade A data for the treatment of osteoarthritis. Therapeutic exercise and TENS showed clinically important benefit for pain and patient global assessment in osteoarthritis. Thermotherapy, ultrasound, and electrical stimulation demonstrated no clinically important benefit for knee osteoarthritis. In summary, there is poor evidence to include or exclude thermotherapy, ultrasound, or electrical stimulation in the treatment of knee osteoarthritis.

With regard to knee tendonitis, the only intervention with significant data was deep transverse friction massage, which showed no clinical benefit. Patellofemoral pain also had 1 grade C intervention recommendation for the use of ultrasound. Further, preoperative exercise, thermotherapy, and TENS showed no clinical benefit for the management of postsurgical knee pain.

The remaining interventions for osteoarthritis of the knee, patellofemoral pain, tendonitis of the knee, and postsurgical pain showed insufficient evidence for the Philadelphia Panel to make guideline recommendations. The major implication of this analysis is that there is poor evidence to support the use of several widely accepted interventions in the treatment of knee pain.

TABLE 3
Summary grid of knee pain guidelines*

Recommendations for neck pain

Acute neck pain is often associated with injury or accident, whereas chronic neck pain is related to repetitive injury. Neck pain is commonly managed with analgesics and rest, but referrals to rehabilitation are increasing. The Philadelphia Panel sought to improve the appropriate use of rehabilitation interventions for neck pain by providing evidence-based guidelines. A summary of the Panel’s recommendations can be found in Table 4.

Only 8 trials met all selection criteria for the management of neck pain. Of these trials, only proprioceptive and therapeutic exercise for chronic neck pain showed clinical benefit for pain and function. The remaining studies showed no clinical benefit or insufficient data. Mechanical traction showed no clinically important benefit in the treatment of acute or chronic neck pain. No further studies that met selection criteria were found with regard to rehabilitation interventions for neck pain. Clearly there are insufficient data in the medical literature with regard to neck pain.

TABLE 4
Summary grid of neck pain guidelines*

Recommendations for shoulder pain

Rehabilitation specialists offer several conservative interventions for the management of shoulder pain. There are few published guidelines for the management of shoulder pain. Results of the analysis are shown in Table 5. As in the analysis of neck pain, the Philadelphia Panel was able to develop a single recommendation with clinical benefit. Clinically important benefit was shown for ultrasound for calcific tendonitis. There was no evidence of clinically important benefit for the use of ultrasound for capsulitis, bursitis, or tendonitis.

TABLE 5
Summary grid of shoulder pain guidelines*

Discussion

By using a rigorous methodology, the Philadelphia Panel has created evidence-based clinical practice guidelines for low back, knee, neck, and shoulder pain rehabilitation based on the current medical literature. Despite the thorough techniques used to create the guidelines, there are methodologic limitations, as with all such reviews. The panel identified many problems with the current body of evidence in the medical literature. The main difficulty with the current literature is the lack of standardization of outcome measurements used in different studies. Future studies need to develop standards of measurement that are valid, reliable, and sensitive to changes in outcome. Further, current studies have used broad inclusion criteria and enrolled patients with diverse etiologies for their pain. Problems with selection and description of patients, definitions of conditions, and standardizations of treatments and outcome measures need to be solved to properly demonstrate benefit from a rehabilitation intervention and remove misclassification bias.

Another limitation is the inherent difficulty of studying rehabilitation interventions. The effectiveness of physical rehabilitation interventions is affected by psychosocial, physical, and occupational factors. These factors can be minimized by fully randomizing large patient groups, thus minimizing selection bias. Another difficulty with developing high-quality randomized controlled trials in the area of rehabilitation is the blinding of patients or caregivers to interventions.

In future studies, it will be necessary to specifically clarify the type and manner of an intervention, intervention intensity and duration, and progression of the intervention according to patient-specific outcomes. Further, a patient typically receives several rehabilitation interventions during a therapy session. These modalities change depending on the phase of recovery (ie, ice, rest, and compression initially, evolving to strengthening, stretching, and electrotherapy with progress). A more thorough means of standardizing this progression in a patient’s care is needed.

In addition, the guidelines did not address cost, patient preferences, or potential harm associated with each intervention for the specific conditions.

Overall, there is a pressing need for further work in the study of rehabilitation interventions, due especially to the increased use of physical therapy for the management of low back pain, knee pain, neck pain, and shoulder pain.

Numerous efforts have been directed toward improving primary care clinicians’ detection of depression since the report of early findings that depressive disorders are common yet often unrecognized in primary care.^1,2 Despite the recent release of a new United States Preventive Task Force recommendation,³ controversy exists about the benefits and cost-effectiveness of routine screening.^4–7

Despite the controversies around depression screening, it is clear that there is significant room for improvement in detection of and treatment outcomes for depression in primary care. Additionally, there is ample evidence from clinical trials that depressed patients with higher severity of illness receive the highest benefit from pharmacological treatment. Therefore, it makes sense to target these highly impaired, depressed patients for detection and treatment.

In previous studies exploring the relationships between symptom severity and diagnostic criteria in a large sample of primary care patients, we found that (1) the Diagnostic and Statistical Manual of Mental Disorders (DSM) criteria for major depression were nonspecific at low levels of impairment but more accurate at high levels, and (2) mood symptom severity assessment performed better than DSM criteria as an independent predictor of impairment and utilization.^8,9 These findings lend support to the notion that case-finding methods incorporating severity in addition to criteria can improve the efficiency of screening in primary care. This study represents our initial exploration of the potential impact of severity-enhanced screening for depression.

We used a retrospective cohort design to answer the following study questions: (1) Can the administration of a symptom severity scale effectively “filter out” a group of patients who meet diagnostic criteria for “threshold” depression but who have less impairment (and may therefore not need treatment)? (2) Does this filtering strategy inappropriately “filter out” patients who are in need of treatment?

Methods

Population and setting

Our sample consisted of 1317 patients presenting for routine care in a university-based family medicine center at the University of Texas Medical Branch (UTMB) in Galveston. The sample, originally recruited for a National Institute for Alcohol Abuse and Alcoholism–funded study of primary care alcohol screening, has been previously described.¹⁰ The study methods and additional data collection methods were reviewed and approved by the UTMB Institutional Review Board.

Evaluation measures

We used the Medical Outcomes Study SF-36 subscales and component summary scale^11,12 to assess health-related quality of life (HRQOL) in all subjects. Medical comorbidity was assessed using electronic medical record review as described previously.⁸ We also examined health care utilization using charge data from the billing system of UTMB. As previously described,⁸ we obtained all inpatient and outpatient charge data for a 15-month period beginning 3 months before the visit at which each subject was surveyed. Outpatient pharmacy data were not included. The results of the charge data subanalysis are presented online in Figure W1, at www.jfponline.com.

Analytic strategy

All subjects were screened with the Clinician Evaluation Guide mood module from the Primary Care Evaluation of Mental Disorders (PRIME-MD).¹³ A “DSM criteria positive” screen included major depressive disorder (MDD), dysthymia, and partial remission of MDD. Symptom severity was assessed using a 6-item Brief Depression Rating (BDR) scale (Table 1) derived from a principal components analysis of 15 mood and anxiety symptom severity questions used in the original study and our subsequent investigations.⁸ Factor analysis of the 6 BDR items confirmed that they occupy a domain distinct from the somatic symptoms included as PRIME-MD depression criteria.

Cronbach’s alpha for the BDR in our sample was 0.8911. Because the distribution of subjects was skewed toward lower severity (median = 9, mean = 10.47, skewness = 1.415), we chose the 75th percentile score¹³ as our cut point for a “positive” BDR. This choice reflected a more conservative definition of severity than the use of a standard cut point of 1 standard deviation above the mean (in this case, a score of 15).

We “filtered out” low-severity patients by matching BDR scores and DSM criteria to create 4 groups for comparison: “low severity and DSM negative,” “high severity only,” “DSM positive only,” and “high severity and DSM positive.”

TABLE 1
Brief Depression Rating*

Data analysis

We used analysis of variance to compare the 4 groups on demographic and outcome measures of interest. We made adjustments where demographic variables or medical comorbidity contributed significantly to the differences between groups by using analysis of covariance (ANCOVA). We examined interaction effects between the covariates and the severity/DSM groups. Where possible and appropriate, we used Bonferroni or Games-Howell adjustments for multiple comparisons between groups.

Results

Size and demographic comparisons

The distribution of the 1317 subjects available for analysis is depicted in Table 2. Fully 75% of the total sample fell below the BDR severity threshold. The BDR filtered out 29% of those subjects meeting DSM criteria because of low symptom severity. Conversely, 17% of subjects who did not meet DSM criteria had high symptom severity based on the BDR. Although the groups had similar demographic characteristics, subjects in the “high severity and DSM positive” group were significantly younger than subjects in the “low severity and DSM negative” group. The distribution of women in all groups was significantly higher than expected except for the “low severity and DSM negative” group. We found even distributions of subjects by ethnicity.

TABLE 2
Group demographics

Mean HRQOL score comparisons

Figure 1 shows mean Mental Health Component Summary (MCS) scores for subjects in the 4 groups, after ANCOVA adjustments for significant covariates (age and African-American ethnicity, P = .003 for both). The groups of subjects that scored either positively or negatively on both the BDR and PRIME-MD occupy opposite poles of very low and very high functional status, respectively. The groups of subjects that scored positively on only the BDR or only the PRIME-MD share the middle ground with no significant difference in MCS-related functional status.

A similar pattern was seen for the Physical Component Summary (PCS) scores from the SF-36. PCS score means ranged from 41.60 to 44.17 among the 4 groups after ANCOVA adjustment for significant covariates (income, medical comorbidity, and Hispanic ethnicity, P < .001 for each). Only the “low severity and DSM negative” and “high severity and DSM positive” groups differed significantly at either end of this range; however, the absolute difference of 2.57 points carries minimal, if any, clinical significance.

Unadjusted mean values from SF-36 subscale scores across the 4 study groups are shown in Figure 2. Although we saw no differences in the “physical functioning” and “role-physical” subscale scores among the groups, a consistent pattern emerged for the remaining 6 subscales. The “high severity and DSM positive” group had significantly lower mean scores (indicating more impairment) than each of the other 3 groups, whereas the “low severity and DSM negative” group had significantly higher scores than each of the other 3 groups. The other 2 groups’ means were in the middle and almost identical across all 8 subscales, indicating that these 2 groups were similar on each SF-36 measure of physical and mental health functioning.

FIGURE 1
Mean deviations from standardized SF-36 subscale norms

FIGURE 2
Mean deviations from standardized SF-36 subscale norms

Mean health care charge comparisons

Briefly, adjusted mean health care charges for each group of subjects showed significant charge differences between groups for the period 3 months before the index visit. The adjusted mean health care charges for this period are shown in Figure W1.

Discussion

We believe that the central findings of this study support a severity-targeted screening strategy. The answer to our first study question—Can the addition of a symptom severity scale effectively “filter out” a group of patients who meet diagnostic criteria for “threshold” depression but have less impairment?—is “yes.” We were able to separate patients meeting criteria for depression into 2 groups, roughly one third with mild symptom severity and roughly two thirds with moderate to severe symptom severity.

The answer to our second question—Does this filtering strategy filter out patients who are in need of treatment?—appears to be “no.” The patterns of HRQOL scores and health care utilization seen for the “filtered-out” patients were indistinguishable from those of a third group of more severely symptomatic patients who did not meet depression criteria at the time of screening and who would not routinely be considered candidates for antidepressant treatment. The presence of a cohort of “middle-ground” patients has been noted in other cross-sectional primary care samples.¹⁴ Whether these patients represent persons with “major depression-in-waiting” or simply distressed and sad individuals is debatable, but there is no evidence to suggest that immediate detection and treatment lead to improved outcomes for these patients. Therefore, in routine clinical practice there would appear to be little risk in failing to identify and treat these patients unless or until their symptom severity increases.

This study does contain some important limitations. First, its cross-sectional nature does not allow us to address important questions about the middle-ground (“high severity only” and “DSM positive only”) patients, such as when they might warrant treatment, whether or when rescreening is useful, or whether “watchful waiting” is the appropriate clinical strategy for these 2 groups. Also, our decision to include as “DSM positive” those patients meeting criteria for dysthymia and MDD in remission deserves a brief explanation. Our previous work with this sample suggested that many patients meeting criteria for these 2 syndromes had high levels of distress and might be thought of as “depressed” by clinicians in routine practice. We included them to make our stratification strategy more closely representative of usual primary care practice. Repeat analyses including only MDD patients as “DSM positive” did not change our primary findings and conclusions, but they did—as expected—decrease the number of subjects in the “positive severity and criteria” group as well as increase the number of subjects in the “high severity only” group.

Despite these limitations, we believe that the results of this study offer hope to practicing physicians trying to cope with the growing depression screening mandate. Primary care physicians seeking to implement depression screening must deal with the fact that depression-screening protocols impose significant burdens on busy clinicians. In the setting of high competing demand^15,16 in primary care, this additional effort—or “cognitive burden”— may render such screening impossible to accomplish in a routine clinical encounter. Several studies support this notion. Rost et al^17,18 found that a screening protocol was not sustainable in primary care, in large part because primary care clinicians were unable to determine which screened patients were most in need of treatment. Dobscha et al¹⁹ found that clinicians failed to adhere to even a limited practice-based screening protocol. Williams et al²⁰ found no difference in treatment rates or short-term outcomes when comparing brief (1-question) and comprehensive (20-question) case-finding protocols with customary clinical care.

Our results suggest that a simple refinement to a screening protocol—ie, using a brief severity measure to target the patients most appropriate for further DSM diagnostic evaluation—could help clinicians in 2 ways. First, it could decrease the burden of positive screening results by one third according to this study. Second, it could provide a more specific “prompt to act” rather than the “prompt to consider” provided by the use of current DSM criteria–based instruments. The importance of this last point should not be underestimated. Valenstein et al²¹ demonstrated that clinicians’ perceptions of the value of positive screen results are closely linked to their likelihood to initiate treatment. If we can enhance the value of the positive prompt, we can improve the rate of response to prompting.

Although we believe that the principle of severity targeting, rather than the specific instrument chosen, will improve screening performance, the instrument must nonetheless be chosen carefully. Kroenke et al²² examined the utility of using the quantitative score from the Patient Health Questionnaire, 9-item version, (PHQ-9) as a severity measure and found that higher scores correlated with lower functional status scores, greater numbers of sick days, and greater health care utilization. However, their methodology included as “positive” only those patients who met diagnostic criteria for MDD. Our use of an independent severity instrument identified an additional 17% of middle-ground patients who might benefit from close observation (“watchful waiting”) without the need for active management.

In summary, we believe that severity-targeted screening represents a promising “next step” in the evolution of office-based screening for depression in primary care. Much more work is needed to determine whether this “prompt to act” will be followed by improved treatment adherence and better treatment outcomes.

Acknowledgments

This project was supported in part by grants from the National Institute on Alcohol Abuse and Alcoholism (No. AA09496) and the Bureau of Health Professions, Health Resources and Services Administration (Nos. D32-PE16033 and D32-PE10158). The authors gratefully acknowledge the valuable feedback of James E. Aikens, PhD, during the preparation of this manuscript.

Numerous efforts have been directed toward improving primary care clinicians’ detection of depression since the report of early findings that depressive disorders are common yet often unrecognized in primary care.^1,2 Despite the recent release of a new United States Preventive Task Force recommendation,³ controversy exists about the benefits and cost-effectiveness of routine screening.^4–7

Despite the controversies around depression screening, it is clear that there is significant room for improvement in detection of and treatment outcomes for depression in primary care. Additionally, there is ample evidence from clinical trials that depressed patients with higher severity of illness receive the highest benefit from pharmacological treatment. Therefore, it makes sense to target these highly impaired, depressed patients for detection and treatment.

In previous studies exploring the relationships between symptom severity and diagnostic criteria in a large sample of primary care patients, we found that (1) the Diagnostic and Statistical Manual of Mental Disorders (DSM) criteria for major depression were nonspecific at low levels of impairment but more accurate at high levels, and (2) mood symptom severity assessment performed better than DSM criteria as an independent predictor of impairment and utilization.^8,9 These findings lend support to the notion that case-finding methods incorporating severity in addition to criteria can improve the efficiency of screening in primary care. This study represents our initial exploration of the potential impact of severity-enhanced screening for depression.

We used a retrospective cohort design to answer the following study questions: (1) Can the administration of a symptom severity scale effectively “filter out” a group of patients who meet diagnostic criteria for “threshold” depression but who have less impairment (and may therefore not need treatment)? (2) Does this filtering strategy inappropriately “filter out” patients who are in need of treatment?

Methods

Population and setting

Our sample consisted of 1317 patients presenting for routine care in a university-based family medicine center at the University of Texas Medical Branch (UTMB) in Galveston. The sample, originally recruited for a National Institute for Alcohol Abuse and Alcoholism–funded study of primary care alcohol screening, has been previously described.¹⁰ The study methods and additional data collection methods were reviewed and approved by the UTMB Institutional Review Board.

Evaluation measures

We used the Medical Outcomes Study SF-36 subscales and component summary scale^11,12 to assess health-related quality of life (HRQOL) in all subjects. Medical comorbidity was assessed using electronic medical record review as described previously.⁸ We also examined health care utilization using charge data from the billing system of UTMB. As previously described,⁸ we obtained all inpatient and outpatient charge data for a 15-month period beginning 3 months before the visit at which each subject was surveyed. Outpatient pharmacy data were not included. The results of the charge data subanalysis are presented online in Figure W1, at www.jfponline.com.

Analytic strategy

All subjects were screened with the Clinician Evaluation Guide mood module from the Primary Care Evaluation of Mental Disorders (PRIME-MD).¹³ A “DSM criteria positive” screen included major depressive disorder (MDD), dysthymia, and partial remission of MDD. Symptom severity was assessed using a 6-item Brief Depression Rating (BDR) scale (Table 1) derived from a principal components analysis of 15 mood and anxiety symptom severity questions used in the original study and our subsequent investigations.⁸ Factor analysis of the 6 BDR items confirmed that they occupy a domain distinct from the somatic symptoms included as PRIME-MD depression criteria.

Cronbach’s alpha for the BDR in our sample was 0.8911. Because the distribution of subjects was skewed toward lower severity (median = 9, mean = 10.47, skewness = 1.415), we chose the 75th percentile score¹³ as our cut point for a “positive” BDR. This choice reflected a more conservative definition of severity than the use of a standard cut point of 1 standard deviation above the mean (in this case, a score of 15).

We “filtered out” low-severity patients by matching BDR scores and DSM criteria to create 4 groups for comparison: “low severity and DSM negative,” “high severity only,” “DSM positive only,” and “high severity and DSM positive.”

TABLE 1
Brief Depression Rating*

Data analysis

We used analysis of variance to compare the 4 groups on demographic and outcome measures of interest. We made adjustments where demographic variables or medical comorbidity contributed significantly to the differences between groups by using analysis of covariance (ANCOVA). We examined interaction effects between the covariates and the severity/DSM groups. Where possible and appropriate, we used Bonferroni or Games-Howell adjustments for multiple comparisons between groups.

Results

Size and demographic comparisons

The distribution of the 1317 subjects available for analysis is depicted in Table 2. Fully 75% of the total sample fell below the BDR severity threshold. The BDR filtered out 29% of those subjects meeting DSM criteria because of low symptom severity. Conversely, 17% of subjects who did not meet DSM criteria had high symptom severity based on the BDR. Although the groups had similar demographic characteristics, subjects in the “high severity and DSM positive” group were significantly younger than subjects in the “low severity and DSM negative” group. The distribution of women in all groups was significantly higher than expected except for the “low severity and DSM negative” group. We found even distributions of subjects by ethnicity.

TABLE 2
Group demographics

Mean HRQOL score comparisons

Figure 1 shows mean Mental Health Component Summary (MCS) scores for subjects in the 4 groups, after ANCOVA adjustments for significant covariates (age and African-American ethnicity, P = .003 for both). The groups of subjects that scored either positively or negatively on both the BDR and PRIME-MD occupy opposite poles of very low and very high functional status, respectively. The groups of subjects that scored positively on only the BDR or only the PRIME-MD share the middle ground with no significant difference in MCS-related functional status.

A similar pattern was seen for the Physical Component Summary (PCS) scores from the SF-36. PCS score means ranged from 41.60 to 44.17 among the 4 groups after ANCOVA adjustment for significant covariates (income, medical comorbidity, and Hispanic ethnicity, P < .001 for each). Only the “low severity and DSM negative” and “high severity and DSM positive” groups differed significantly at either end of this range; however, the absolute difference of 2.57 points carries minimal, if any, clinical significance.

Unadjusted mean values from SF-36 subscale scores across the 4 study groups are shown in Figure 2. Although we saw no differences in the “physical functioning” and “role-physical” subscale scores among the groups, a consistent pattern emerged for the remaining 6 subscales. The “high severity and DSM positive” group had significantly lower mean scores (indicating more impairment) than each of the other 3 groups, whereas the “low severity and DSM negative” group had significantly higher scores than each of the other 3 groups. The other 2 groups’ means were in the middle and almost identical across all 8 subscales, indicating that these 2 groups were similar on each SF-36 measure of physical and mental health functioning.

FIGURE 1
Mean deviations from standardized SF-36 subscale norms

FIGURE 2
Mean deviations from standardized SF-36 subscale norms

Mean health care charge comparisons

Briefly, adjusted mean health care charges for each group of subjects showed significant charge differences between groups for the period 3 months before the index visit. The adjusted mean health care charges for this period are shown in Figure W1.

Discussion

We believe that the central findings of this study support a severity-targeted screening strategy. The answer to our first study question—Can the addition of a symptom severity scale effectively “filter out” a group of patients who meet diagnostic criteria for “threshold” depression but have less impairment?—is “yes.” We were able to separate patients meeting criteria for depression into 2 groups, roughly one third with mild symptom severity and roughly two thirds with moderate to severe symptom severity.

The answer to our second question—Does this filtering strategy filter out patients who are in need of treatment?—appears to be “no.” The patterns of HRQOL scores and health care utilization seen for the “filtered-out” patients were indistinguishable from those of a third group of more severely symptomatic patients who did not meet depression criteria at the time of screening and who would not routinely be considered candidates for antidepressant treatment. The presence of a cohort of “middle-ground” patients has been noted in other cross-sectional primary care samples.¹⁴ Whether these patients represent persons with “major depression-in-waiting” or simply distressed and sad individuals is debatable, but there is no evidence to suggest that immediate detection and treatment lead to improved outcomes for these patients. Therefore, in routine clinical practice there would appear to be little risk in failing to identify and treat these patients unless or until their symptom severity increases.

This study does contain some important limitations. First, its cross-sectional nature does not allow us to address important questions about the middle-ground (“high severity only” and “DSM positive only”) patients, such as when they might warrant treatment, whether or when rescreening is useful, or whether “watchful waiting” is the appropriate clinical strategy for these 2 groups. Also, our decision to include as “DSM positive” those patients meeting criteria for dysthymia and MDD in remission deserves a brief explanation. Our previous work with this sample suggested that many patients meeting criteria for these 2 syndromes had high levels of distress and might be thought of as “depressed” by clinicians in routine practice. We included them to make our stratification strategy more closely representative of usual primary care practice. Repeat analyses including only MDD patients as “DSM positive” did not change our primary findings and conclusions, but they did—as expected—decrease the number of subjects in the “positive severity and criteria” group as well as increase the number of subjects in the “high severity only” group.

Despite these limitations, we believe that the results of this study offer hope to practicing physicians trying to cope with the growing depression screening mandate. Primary care physicians seeking to implement depression screening must deal with the fact that depression-screening protocols impose significant burdens on busy clinicians. In the setting of high competing demand^15,16 in primary care, this additional effort—or “cognitive burden”— may render such screening impossible to accomplish in a routine clinical encounter. Several studies support this notion. Rost et al^17,18 found that a screening protocol was not sustainable in primary care, in large part because primary care clinicians were unable to determine which screened patients were most in need of treatment. Dobscha et al¹⁹ found that clinicians failed to adhere to even a limited practice-based screening protocol. Williams et al²⁰ found no difference in treatment rates or short-term outcomes when comparing brief (1-question) and comprehensive (20-question) case-finding protocols with customary clinical care.

Our results suggest that a simple refinement to a screening protocol—ie, using a brief severity measure to target the patients most appropriate for further DSM diagnostic evaluation—could help clinicians in 2 ways. First, it could decrease the burden of positive screening results by one third according to this study. Second, it could provide a more specific “prompt to act” rather than the “prompt to consider” provided by the use of current DSM criteria–based instruments. The importance of this last point should not be underestimated. Valenstein et al²¹ demonstrated that clinicians’ perceptions of the value of positive screen results are closely linked to their likelihood to initiate treatment. If we can enhance the value of the positive prompt, we can improve the rate of response to prompting.

Although we believe that the principle of severity targeting, rather than the specific instrument chosen, will improve screening performance, the instrument must nonetheless be chosen carefully. Kroenke et al²² examined the utility of using the quantitative score from the Patient Health Questionnaire, 9-item version, (PHQ-9) as a severity measure and found that higher scores correlated with lower functional status scores, greater numbers of sick days, and greater health care utilization. However, their methodology included as “positive” only those patients who met diagnostic criteria for MDD. Our use of an independent severity instrument identified an additional 17% of middle-ground patients who might benefit from close observation (“watchful waiting”) without the need for active management.

In summary, we believe that severity-targeted screening represents a promising “next step” in the evolution of office-based screening for depression in primary care. Much more work is needed to determine whether this “prompt to act” will be followed by improved treatment adherence and better treatment outcomes.

Acknowledgments

This project was supported in part by grants from the National Institute on Alcohol Abuse and Alcoholism (No. AA09496) and the Bureau of Health Professions, Health Resources and Services Administration (Nos. D32-PE16033 and D32-PE10158). The authors gratefully acknowledge the valuable feedback of James E. Aikens, PhD, during the preparation of this manuscript.

Numerous efforts have been directed toward improving primary care clinicians’ detection of depression since the report of early findings that depressive disorders are common yet often unrecognized in primary care.^1,2 Despite the recent release of a new United States Preventive Task Force recommendation,³ controversy exists about the benefits and cost-effectiveness of routine screening.^4–7

Despite the controversies around depression screening, it is clear that there is significant room for improvement in detection of and treatment outcomes for depression in primary care. Additionally, there is ample evidence from clinical trials that depressed patients with higher severity of illness receive the highest benefit from pharmacological treatment. Therefore, it makes sense to target these highly impaired, depressed patients for detection and treatment.

In previous studies exploring the relationships between symptom severity and diagnostic criteria in a large sample of primary care patients, we found that (1) the Diagnostic and Statistical Manual of Mental Disorders (DSM) criteria for major depression were nonspecific at low levels of impairment but more accurate at high levels, and (2) mood symptom severity assessment performed better than DSM criteria as an independent predictor of impairment and utilization.^8,9 These findings lend support to the notion that case-finding methods incorporating severity in addition to criteria can improve the efficiency of screening in primary care. This study represents our initial exploration of the potential impact of severity-enhanced screening for depression.

We used a retrospective cohort design to answer the following study questions: (1) Can the administration of a symptom severity scale effectively “filter out” a group of patients who meet diagnostic criteria for “threshold” depression but who have less impairment (and may therefore not need treatment)? (2) Does this filtering strategy inappropriately “filter out” patients who are in need of treatment?

Methods

Population and setting

Our sample consisted of 1317 patients presenting for routine care in a university-based family medicine center at the University of Texas Medical Branch (UTMB) in Galveston. The sample, originally recruited for a National Institute for Alcohol Abuse and Alcoholism–funded study of primary care alcohol screening, has been previously described.¹⁰ The study methods and additional data collection methods were reviewed and approved by the UTMB Institutional Review Board.

Evaluation measures

We used the Medical Outcomes Study SF-36 subscales and component summary scale^11,12 to assess health-related quality of life (HRQOL) in all subjects. Medical comorbidity was assessed using electronic medical record review as described previously.⁸ We also examined health care utilization using charge data from the billing system of UTMB. As previously described,⁸ we obtained all inpatient and outpatient charge data for a 15-month period beginning 3 months before the visit at which each subject was surveyed. Outpatient pharmacy data were not included. The results of the charge data subanalysis are presented online in Figure W1, at www.jfponline.com.

Analytic strategy

All subjects were screened with the Clinician Evaluation Guide mood module from the Primary Care Evaluation of Mental Disorders (PRIME-MD).¹³ A “DSM criteria positive” screen included major depressive disorder (MDD), dysthymia, and partial remission of MDD. Symptom severity was assessed using a 6-item Brief Depression Rating (BDR) scale (Table 1) derived from a principal components analysis of 15 mood and anxiety symptom severity questions used in the original study and our subsequent investigations.⁸ Factor analysis of the 6 BDR items confirmed that they occupy a domain distinct from the somatic symptoms included as PRIME-MD depression criteria.

Cronbach’s alpha for the BDR in our sample was 0.8911. Because the distribution of subjects was skewed toward lower severity (median = 9, mean = 10.47, skewness = 1.415), we chose the 75th percentile score¹³ as our cut point for a “positive” BDR. This choice reflected a more conservative definition of severity than the use of a standard cut point of 1 standard deviation above the mean (in this case, a score of 15).

We “filtered out” low-severity patients by matching BDR scores and DSM criteria to create 4 groups for comparison: “low severity and DSM negative,” “high severity only,” “DSM positive only,” and “high severity and DSM positive.”

TABLE 1
Brief Depression Rating*

Data analysis

We used analysis of variance to compare the 4 groups on demographic and outcome measures of interest. We made adjustments where demographic variables or medical comorbidity contributed significantly to the differences between groups by using analysis of covariance (ANCOVA). We examined interaction effects between the covariates and the severity/DSM groups. Where possible and appropriate, we used Bonferroni or Games-Howell adjustments for multiple comparisons between groups.

Results

Size and demographic comparisons

The distribution of the 1317 subjects available for analysis is depicted in Table 2. Fully 75% of the total sample fell below the BDR severity threshold. The BDR filtered out 29% of those subjects meeting DSM criteria because of low symptom severity. Conversely, 17% of subjects who did not meet DSM criteria had high symptom severity based on the BDR. Although the groups had similar demographic characteristics, subjects in the “high severity and DSM positive” group were significantly younger than subjects in the “low severity and DSM negative” group. The distribution of women in all groups was significantly higher than expected except for the “low severity and DSM negative” group. We found even distributions of subjects by ethnicity.

TABLE 2
Group demographics

Mean HRQOL score comparisons

Figure 1 shows mean Mental Health Component Summary (MCS) scores for subjects in the 4 groups, after ANCOVA adjustments for significant covariates (age and African-American ethnicity, P = .003 for both). The groups of subjects that scored either positively or negatively on both the BDR and PRIME-MD occupy opposite poles of very low and very high functional status, respectively. The groups of subjects that scored positively on only the BDR or only the PRIME-MD share the middle ground with no significant difference in MCS-related functional status.

A similar pattern was seen for the Physical Component Summary (PCS) scores from the SF-36. PCS score means ranged from 41.60 to 44.17 among the 4 groups after ANCOVA adjustment for significant covariates (income, medical comorbidity, and Hispanic ethnicity, P < .001 for each). Only the “low severity and DSM negative” and “high severity and DSM positive” groups differed significantly at either end of this range; however, the absolute difference of 2.57 points carries minimal, if any, clinical significance.

Unadjusted mean values from SF-36 subscale scores across the 4 study groups are shown in Figure 2. Although we saw no differences in the “physical functioning” and “role-physical” subscale scores among the groups, a consistent pattern emerged for the remaining 6 subscales. The “high severity and DSM positive” group had significantly lower mean scores (indicating more impairment) than each of the other 3 groups, whereas the “low severity and DSM negative” group had significantly higher scores than each of the other 3 groups. The other 2 groups’ means were in the middle and almost identical across all 8 subscales, indicating that these 2 groups were similar on each SF-36 measure of physical and mental health functioning.

FIGURE 1
Mean deviations from standardized SF-36 subscale norms

FIGURE 2
Mean deviations from standardized SF-36 subscale norms

Mean health care charge comparisons

Briefly, adjusted mean health care charges for each group of subjects showed significant charge differences between groups for the period 3 months before the index visit. The adjusted mean health care charges for this period are shown in Figure W1.

Discussion

We believe that the central findings of this study support a severity-targeted screening strategy. The answer to our first study question—Can the addition of a symptom severity scale effectively “filter out” a group of patients who meet diagnostic criteria for “threshold” depression but have less impairment?—is “yes.” We were able to separate patients meeting criteria for depression into 2 groups, roughly one third with mild symptom severity and roughly two thirds with moderate to severe symptom severity.

The answer to our second question—Does this filtering strategy filter out patients who are in need of treatment?—appears to be “no.” The patterns of HRQOL scores and health care utilization seen for the “filtered-out” patients were indistinguishable from those of a third group of more severely symptomatic patients who did not meet depression criteria at the time of screening and who would not routinely be considered candidates for antidepressant treatment. The presence of a cohort of “middle-ground” patients has been noted in other cross-sectional primary care samples.¹⁴ Whether these patients represent persons with “major depression-in-waiting” or simply distressed and sad individuals is debatable, but there is no evidence to suggest that immediate detection and treatment lead to improved outcomes for these patients. Therefore, in routine clinical practice there would appear to be little risk in failing to identify and treat these patients unless or until their symptom severity increases.

This study does contain some important limitations. First, its cross-sectional nature does not allow us to address important questions about the middle-ground (“high severity only” and “DSM positive only”) patients, such as when they might warrant treatment, whether or when rescreening is useful, or whether “watchful waiting” is the appropriate clinical strategy for these 2 groups. Also, our decision to include as “DSM positive” those patients meeting criteria for dysthymia and MDD in remission deserves a brief explanation. Our previous work with this sample suggested that many patients meeting criteria for these 2 syndromes had high levels of distress and might be thought of as “depressed” by clinicians in routine practice. We included them to make our stratification strategy more closely representative of usual primary care practice. Repeat analyses including only MDD patients as “DSM positive” did not change our primary findings and conclusions, but they did—as expected—decrease the number of subjects in the “positive severity and criteria” group as well as increase the number of subjects in the “high severity only” group.

Despite these limitations, we believe that the results of this study offer hope to practicing physicians trying to cope with the growing depression screening mandate. Primary care physicians seeking to implement depression screening must deal with the fact that depression-screening protocols impose significant burdens on busy clinicians. In the setting of high competing demand^15,16 in primary care, this additional effort—or “cognitive burden”— may render such screening impossible to accomplish in a routine clinical encounter. Several studies support this notion. Rost et al^17,18 found that a screening protocol was not sustainable in primary care, in large part because primary care clinicians were unable to determine which screened patients were most in need of treatment. Dobscha et al¹⁹ found that clinicians failed to adhere to even a limited practice-based screening protocol. Williams et al²⁰ found no difference in treatment rates or short-term outcomes when comparing brief (1-question) and comprehensive (20-question) case-finding protocols with customary clinical care.

Our results suggest that a simple refinement to a screening protocol—ie, using a brief severity measure to target the patients most appropriate for further DSM diagnostic evaluation—could help clinicians in 2 ways. First, it could decrease the burden of positive screening results by one third according to this study. Second, it could provide a more specific “prompt to act” rather than the “prompt to consider” provided by the use of current DSM criteria–based instruments. The importance of this last point should not be underestimated. Valenstein et al²¹ demonstrated that clinicians’ perceptions of the value of positive screen results are closely linked to their likelihood to initiate treatment. If we can enhance the value of the positive prompt, we can improve the rate of response to prompting.

Although we believe that the principle of severity targeting, rather than the specific instrument chosen, will improve screening performance, the instrument must nonetheless be chosen carefully. Kroenke et al²² examined the utility of using the quantitative score from the Patient Health Questionnaire, 9-item version, (PHQ-9) as a severity measure and found that higher scores correlated with lower functional status scores, greater numbers of sick days, and greater health care utilization. However, their methodology included as “positive” only those patients who met diagnostic criteria for MDD. Our use of an independent severity instrument identified an additional 17% of middle-ground patients who might benefit from close observation (“watchful waiting”) without the need for active management.

In summary, we believe that severity-targeted screening represents a promising “next step” in the evolution of office-based screening for depression in primary care. Much more work is needed to determine whether this “prompt to act” will be followed by improved treatment adherence and better treatment outcomes.

Acknowledgments

This project was supported in part by grants from the National Institute on Alcohol Abuse and Alcoholism (No. AA09496) and the Bureau of Health Professions, Health Resources and Services Administration (Nos. D32-PE16033 and D32-PE10158). The authors gratefully acknowledge the valuable feedback of James E. Aikens, PhD, during the preparation of this manuscript.

Estrogen-containing hormone replacement therapy (ERT) after menopause has been implicated as a causal factor in the development of primary breast cancer.^1,2 Fearing cancer recurrence, most physicians do not offer ERT to postmenopausal women with a history of breast cancer. However, estrogen deficiency, which is especially common in women after chemotherapy, can be associated with severe symptoms, reduced quality of life, and increased risk of osteoporosis and possibly coronary artery disease. Although there are theoretical justifications to discourage the use of ERT by women at high risk for breast cancer, there is little objective evidence that hormone replacement increases the likelihood of breast cancer recurrence or of mortality among survivors of primary breast cancer. It is difficult for clinicians and patients to make rational decisions regarding ERT in these patients, given the paucity of studies and the difficulty of interpreting the few studies available.

Several observational studies have been published on the use of estrogen and/or combined estrogen–progesterone hormone replacement therapy in women who have had breast cancer. Many of these studies have reported single-institution series of outcomes among survivors who opted to take ERT for their menopausal symptoms. These studies tend to demonstrate rather unimpressive incidences of recurrence and mortality events. However, it is possible that such studies underestimate the risks because patients who are given ERT may represent a subgroup with a better prognosis than other patients (bias by indication). A smaller number of studies has used comparison groups and attempted to control for disease severity and other factors associated with recurrence.

We conducted a meta-analysis of studies comparing women who used ERT after the diagnosis of breast cancer with a control group of non-ERT users to determine whether ERT is associated with an increased risk of cancer recurrence or all-cause mortality among breast cancer survivors.

Methods

Search strategy

We identified relevant studies through independent literature searches of Medline (from 1966 to August 2001) and Cancerlit (from 1986 to August 2001) with the use of OVID software and the following search terms: estrogen replacement therapy, hormone replacement therapy, breast neoplasms, neoplasm recurrence, survivors. No language restriction was imposed. A careful review of titles and abstracts was done to identify relevant articles, and for these, the full articles were retrieved for review. Bibliographies of identified studies and review articles were examined for additional citations. Medline and Cancerlit databases were also searched by the names of authors of relevant studies to identify any missed articles. The authors of large studies and experts from our institution were asked to review the reference list for completeness and to suggest sources of unpublished data.

Inclusion criteria

Studies were considered for inclusion into the meta-analysis if they met the following criteria: (1) the population studied was women with a previous diagnosis of breast cancer, (2) the risk factor considered was the use of systemic estrogen or any combination hormone replacement therapy that included estrogen, (3) the outcome measured included the recurrence of breast cancer (whether a new or recurring primary cancer) and/or mortality, and (4) the study design was a randomized controlled trial or cohort study comparing women who used ERT after their breast cancer diagnosis with a concurrent, historical, or population-based control group of women who did not. Single-arm cohort studies were retrieved and summarized qualitatively but not included in the statistical analysis. If more than 1 publication was identified which reported the same data, the study with the most recent or complete data was selected for the analysis. We independently reviewed all studies for inclusion, and any differences were resolved through consensus.

Validity assessment

All included studies were assessed for validity by 2 independent reviewers, blinded to study results, for the following characteristics: (1) prospective data collection, (2) clear subject inclusion criteria, (3) reliability of exposure, (4) similarity between exposed and unexposed groups, (5) loss to follow-up, and (6) reliability of outcome assessment. When threats to study validity were identified, attempts were made to determine whether these threats were likely to significantly influence the results of the study and to estimate the direction of the influence of these threats on the resulting data. Because baseline differences between the study groups are such an important threat to the validity of these studies, the studies were graded as higher quality and lower quality based on whether significant differences in known prognostic factors existed.

Data management and analysis

A data extraction form was created to aid consistent recording of data from all studies, and both investigators extracted data independently. Any discrepancies in data interpretation or abstraction were resolved through consensus. Study characteristics and results for single-arm cohort studies were presented descriptively. For controlled studies, data were entered as dichotomous variables into Review Manager 4.1 software, as distributed by the Cochrane Collaboration. Summary relative risk (RR) estimates were calculated by using a fixed effects model (Mantel-Haenszel method) unless the results were found to be statistically heterogeneous (P < .1) through the use of a Q statistic, in which case the more conservative random effects model (DerSimonian-Laird method) was used. A subanalysis was performed based on the quality ratings, with a lower rating given to studies in which the exposed and unexposed groups differed significantly on important prognostic factors such as age, tumor stage, and time since diagnosis. Funnel plots were constructed to identify possible publication bias.

Results

Description of studies

The original search yielded 24 relevant reports, including 1 unpublished report (Bluming AZ, personal communication, 2000) with 2 separate studies. One of these and 12 published single-arm cohort studies^3-14 were excluded because they lacked a control group, but a summary of these studies can be found online (Table W1, available on the JFP Web site: www.jfponline.com). Twelve reports^15-25 met the inclusion criteria and provided data comparing the rates of recurrence or mortality among patients who used ERT after the diagnosis of breast cancer and users vs controls. Among these studies were 8 independent cohort studies from the published literature,^{15-17,20,21,23-25} one set of unpublished data from Bluming et al, and one 6-month pilot randomized controlled trial.¹⁹ One matched cohort study¹⁸ presented recurrence data for 90 patients and 180 controls who were later included in a larger, non-matched study reporting recurrence and mortality.¹⁵ Another small study²² reported only deaths from breast cancer from a data set included at least in part in another report¹⁶ and was therefore excluded. Overall, the included studies accounted for 717 subjects who used hormone replacement therapy at some time after their diagnosis of breast cancer compared with 2545 nonusers. Characteristics of included studies are summarized in the Table.

TABLE
Characteristics of included studies

Methodologic quality

The quality of the studies was variable. The only randomized controlled trial¹⁹ was a 6-month pilot study, after which the allocation code was broken and patients were free to choose whether to be on treatment. Of the cohort studies, only 1 trial²¹ began with an inception cohort that combined data from 62 patients who elected to be part of a randomized controlled trial with that from another 257 who declined to be randomized but chose on their own whether to take ERT.²¹ One study was clearly retrospective²³ ; patients with ductal carcinoma in situ were identified through a cancer registry, and their exposures and recurrences were determined through a mailed questionnaire. The remaining studies used clinic records to identify patients who had been prescribed ERT and compared those recurrence and mortality rates with those of a control group comprising the remaining clinic patients^{15,18,20,24,25} or matched subjects selected from a regional cancer surveillance database.^15,16 Although the matching process controlled for some important prognostic factors (age, stage, and time since diagnosis), post-diagnosis ERT use was not recorded in the surveillance database, so these control groups may have contained patients who took ERT at some time, thereby diluting any differences that might be observed. Conversely, none of the cohort studies reported means confirming that those for whom HRT had been prescribed actually took it regularly.

Across all studies, the studied interventions included a systemic estrogen, usually in combination with progesterone unless the subject had had a hysterectomy. The mean age at diagnosis of cancer varied among studies, from 42 to 65 years. There was also wide variability among subjects between and within the studies with regard to disease-free interval (the time between diagnosis of cancer and initiating ERT), duration of ERT use, and length of follow-up (Table). A few studies matched controls to ERT users based on these variables^16-18,24 or demonstrated that the groups were comparable.^19,21 In no study were subjects matched on type of treatment, race, estrogen receptor status, smoking, or other potentially important prognostic factors. Estrogen receptor status was unavailable for a large number of patients in these studies and could not be used for comparison.

Several studies contained methodologic flaws that resulted in important differences between comparison groups. Bluming and colleagues provided an unpublished analysis of recurrences in a sample of ERT users with previous T1N0 (stage I) cancers compared with a separate data set of similar patients who did not use ERT. In that study, tumor size was not known for 62% of the control group and 36% of the ERT group. Median follow-up was shorter in the ERT group, the tumors were smaller, the diagnoses were later, and patients were more likely to have received chemotherapy. Natrajan et al²⁰ compared 50 ERT users with 18 nonusers who left their clinic and were followed elsewhere. ERT users were younger than the nonusers and had longer follow-up. Little information was given regarding the cancer stages of the nonusers, and this was the only study primarily using hormone pellets and combining estrogen with testosterone in most patients. Habel et al²³ included only patients with ductal carcinoma in situ in a retrospective cohort study in which exposure was ascertained by mailed survey. Only 67% responded to the survey, and no baseline data comparing the ERT users with nonusers on important prognostic factors were provided. In a study by Beckman et al,²⁵ users were younger and less likely than nonusers to have grade 3 cancer (16% vs 30%), although this difference was reported to be nonsignificant. Median duration of follow-up was also longer in nonusers than in users (42 vs 37 months). In an unmatched study¹⁵ of ERT users and nonusers from the same practices in Australia, significant differences were found between groups in age, stage, and type of treatment rendered.

Because of the strong potential for bias due to baseline differences in risk of breast cancer recurrence, subanalyses included only those studies for which differences in important prognostic factors were not apparent.^16-19,21,24 In the case of the Australian study, a subset of the data, matched 2:1 on age, node status, tumor diameter, disease-free interval, and year of diagnosis, was found in an earlier report¹⁸ and used in the subanalysis.

Meta-analysis results

Overall, 8 studies reported the recurrence of breast cancer as an outcome. A meta-analysis of these studies showed that breast cancer survivors using ERT experienced no increase in the risk of recurrence compared with nonusers (8.2% vs 10.2%; RR, 0.72, 95% confidence interval [CI], 0.47–1.10). Because no statistical heterogeneity was demonstrated, a fixed effects model was used. Studies were analyzed separately depending on whether patients were matched or reportedly similar on factors such as age at diagnosis, tumor stage, and disease-free interval. Results were similar (Figure 1).

Six studies were included in a combined analysis of overall mortality (Figure 2). The ERT users in these studies experienced significantly fewer deaths (3.0%) than the nonusers (11.4%) over the combined study periods (RR, 0.18; 95% CI, 0.10–0.31; numbers needed to treat = 12). Subanalyses of those studies in which groups were comparable showed similar results (RR, 0.21; 95% CI, 0.10–0.46).

Despite the variability in study designs and subjects, all tests for heterogeneity were nonsignificant. In addition, funnel plots showed no evidence of publication bias (Figure W1, available on the JFP Web site: www.jfponline.com).

All studies, controlled or not, that reported data on control of menopausal symptoms reported significant benefit with ERT.^{2,7-9,11,19,25}

FIGURE 1
Graphic summary of studies on recurrence of breast cancer in ERT users vs nonusers

FIGURE 2
Graphic summary of studies of total mortality among users vs nonusers of estrogen replacement therapy

Discussion

This meta-analysis of observational studies in breast cancer survivors refutes the hypothesis that ERT increases the risk of breast cancer recurrence and suggests that it may in fact reduce all-cause mortality. However, conclusions drawn from observational studies can be seriously limited by potential sources of bias. For example, the studies likely had a bias by indication. That is, patients with more aggressive prognostic factors may not have been prescribed ERT, thereby making the treatment group likely to have represented a subgroup with a lower risk of recurrence than the general population used for comparison. However, several studies matched controls on important prognostic factors, and elimination of the unmatched study did not significantly affect study results. Similarly, in the absence of randomization, unmeasured confounders may have played a role. The treatment and control groups might have differed on other predictors of mortality that were not considered, such as in a healthy user effect in which subjects on ERT may have been more informed of its benefits and followed other, more healthy lifestyle behaviors than the comparison groups. They also may have been followed more closely by their physicians than the average breast cancer survivor.

In general, the subjects of the included studies over-represented patients with lower severity of disease than the general population of breast cancer survivors. Few studies included any subjects with a history of stage IV cancer (1 case with distant metastases), and several included patients with stage II or lower. Therefore, the results of this systematic review may be best generalized only to patients with lower stage disease. In addition, although subjects used ERT for as long as 32 years, the average duration of ERT use was shorter than 4 years in all but 1 study; longer follow-up is needed to truly assess the long-term effects of ERT in these high-risk patients. Available published studies also do not provide the detail needed to explore the potential contributions of estrogen receptor status or concomitant tamoxifen use.

Our finding of no significant difference in cancer recurrence associated with ERT use among patients with breast cancer is consistent with that of another recent meta-analysis.²⁶ Those researchers constructed expected control groups by using the average disease free interval before starting ERT, and known nodal status distribution from several single-arm cohort studies to calculate relative risks of recurrence for these studies. This method introduces additional bias and several assumptions that may not be warranted. For instance, risk of recurrence is much higher in the first few years after treatment for primary breast cancer. Therefore, the remarkable variability in the disease-free intervals and duration of follow-up among subjects within each of these studies make it very difficult to estimate expected recurrence rates without the detailed individual data from the original studies. Despite the “within-study” and “between-study” variabilities, the results of the individual studies are quite similar.

Observational studies, although limited, do not hold the ethical problems inherent to randomized controlled trials and are especially appropriate with a treatment as controversial as estrogen in breast cancer survivors. Available studies have produced findings contrary to conventional belief and to the theory that likens ERT to “fuel on the fire” in breast cancer. Such a theory has, until recently, made it seem unethical to justify a randomized controlled trial of ERT in these patients. However, data from some of these individual studies have provided enough support that enrollment for such trials have begun.²⁷ Previous studies of breast cancer risk with estrogen use have suggested that more than 10 years of treatment are required to see an increase in primary breast cancer,²⁸ so we may not have definitive evidence for some time. Meanwhile, there is no compelling evidence to support universal withholding of estrogen from well-informed women with symptomatic menopause, particularly among survivors of low-stage breast cancer.

Estrogen-containing hormone replacement therapy (ERT) after menopause has been implicated as a causal factor in the development of primary breast cancer.^1,2 Fearing cancer recurrence, most physicians do not offer ERT to postmenopausal women with a history of breast cancer. However, estrogen deficiency, which is especially common in women after chemotherapy, can be associated with severe symptoms, reduced quality of life, and increased risk of osteoporosis and possibly coronary artery disease. Although there are theoretical justifications to discourage the use of ERT by women at high risk for breast cancer, there is little objective evidence that hormone replacement increases the likelihood of breast cancer recurrence or of mortality among survivors of primary breast cancer. It is difficult for clinicians and patients to make rational decisions regarding ERT in these patients, given the paucity of studies and the difficulty of interpreting the few studies available.

Several observational studies have been published on the use of estrogen and/or combined estrogen–progesterone hormone replacement therapy in women who have had breast cancer. Many of these studies have reported single-institution series of outcomes among survivors who opted to take ERT for their menopausal symptoms. These studies tend to demonstrate rather unimpressive incidences of recurrence and mortality events. However, it is possible that such studies underestimate the risks because patients who are given ERT may represent a subgroup with a better prognosis than other patients (bias by indication). A smaller number of studies has used comparison groups and attempted to control for disease severity and other factors associated with recurrence.

We conducted a meta-analysis of studies comparing women who used ERT after the diagnosis of breast cancer with a control group of non-ERT users to determine whether ERT is associated with an increased risk of cancer recurrence or all-cause mortality among breast cancer survivors.

Methods

Search strategy

We identified relevant studies through independent literature searches of Medline (from 1966 to August 2001) and Cancerlit (from 1986 to August 2001) with the use of OVID software and the following search terms: estrogen replacement therapy, hormone replacement therapy, breast neoplasms, neoplasm recurrence, survivors. No language restriction was imposed. A careful review of titles and abstracts was done to identify relevant articles, and for these, the full articles were retrieved for review. Bibliographies of identified studies and review articles were examined for additional citations. Medline and Cancerlit databases were also searched by the names of authors of relevant studies to identify any missed articles. The authors of large studies and experts from our institution were asked to review the reference list for completeness and to suggest sources of unpublished data.

Inclusion criteria

Studies were considered for inclusion into the meta-analysis if they met the following criteria: (1) the population studied was women with a previous diagnosis of breast cancer, (2) the risk factor considered was the use of systemic estrogen or any combination hormone replacement therapy that included estrogen, (3) the outcome measured included the recurrence of breast cancer (whether a new or recurring primary cancer) and/or mortality, and (4) the study design was a randomized controlled trial or cohort study comparing women who used ERT after their breast cancer diagnosis with a concurrent, historical, or population-based control group of women who did not. Single-arm cohort studies were retrieved and summarized qualitatively but not included in the statistical analysis. If more than 1 publication was identified which reported the same data, the study with the most recent or complete data was selected for the analysis. We independently reviewed all studies for inclusion, and any differences were resolved through consensus.

Validity assessment

All included studies were assessed for validity by 2 independent reviewers, blinded to study results, for the following characteristics: (1) prospective data collection, (2) clear subject inclusion criteria, (3) reliability of exposure, (4) similarity between exposed and unexposed groups, (5) loss to follow-up, and (6) reliability of outcome assessment. When threats to study validity were identified, attempts were made to determine whether these threats were likely to significantly influence the results of the study and to estimate the direction of the influence of these threats on the resulting data. Because baseline differences between the study groups are such an important threat to the validity of these studies, the studies were graded as higher quality and lower quality based on whether significant differences in known prognostic factors existed.

Data management and analysis

A data extraction form was created to aid consistent recording of data from all studies, and both investigators extracted data independently. Any discrepancies in data interpretation or abstraction were resolved through consensus. Study characteristics and results for single-arm cohort studies were presented descriptively. For controlled studies, data were entered as dichotomous variables into Review Manager 4.1 software, as distributed by the Cochrane Collaboration. Summary relative risk (RR) estimates were calculated by using a fixed effects model (Mantel-Haenszel method) unless the results were found to be statistically heterogeneous (P < .1) through the use of a Q statistic, in which case the more conservative random effects model (DerSimonian-Laird method) was used. A subanalysis was performed based on the quality ratings, with a lower rating given to studies in which the exposed and unexposed groups differed significantly on important prognostic factors such as age, tumor stage, and time since diagnosis. Funnel plots were constructed to identify possible publication bias.

Results

Description of studies

The original search yielded 24 relevant reports, including 1 unpublished report (Bluming AZ, personal communication, 2000) with 2 separate studies. One of these and 12 published single-arm cohort studies^3-14 were excluded because they lacked a control group, but a summary of these studies can be found online (Table W1, available on the JFP Web site: www.jfponline.com). Twelve reports^15-25 met the inclusion criteria and provided data comparing the rates of recurrence or mortality among patients who used ERT after the diagnosis of breast cancer and users vs controls. Among these studies were 8 independent cohort studies from the published literature,^{15-17,20,21,23-25} one set of unpublished data from Bluming et al, and one 6-month pilot randomized controlled trial.¹⁹ One matched cohort study¹⁸ presented recurrence data for 90 patients and 180 controls who were later included in a larger, non-matched study reporting recurrence and mortality.¹⁵ Another small study²² reported only deaths from breast cancer from a data set included at least in part in another report¹⁶ and was therefore excluded. Overall, the included studies accounted for 717 subjects who used hormone replacement therapy at some time after their diagnosis of breast cancer compared with 2545 nonusers. Characteristics of included studies are summarized in the Table.

TABLE
Characteristics of included studies

Methodologic quality

The quality of the studies was variable. The only randomized controlled trial¹⁹ was a 6-month pilot study, after which the allocation code was broken and patients were free to choose whether to be on treatment. Of the cohort studies, only 1 trial²¹ began with an inception cohort that combined data from 62 patients who elected to be part of a randomized controlled trial with that from another 257 who declined to be randomized but chose on their own whether to take ERT.²¹ One study was clearly retrospective²³ ; patients with ductal carcinoma in situ were identified through a cancer registry, and their exposures and recurrences were determined through a mailed questionnaire. The remaining studies used clinic records to identify patients who had been prescribed ERT and compared those recurrence and mortality rates with those of a control group comprising the remaining clinic patients^{15,18,20,24,25} or matched subjects selected from a regional cancer surveillance database.^15,16 Although the matching process controlled for some important prognostic factors (age, stage, and time since diagnosis), post-diagnosis ERT use was not recorded in the surveillance database, so these control groups may have contained patients who took ERT at some time, thereby diluting any differences that might be observed. Conversely, none of the cohort studies reported means confirming that those for whom HRT had been prescribed actually took it regularly.

Across all studies, the studied interventions included a systemic estrogen, usually in combination with progesterone unless the subject had had a hysterectomy. The mean age at diagnosis of cancer varied among studies, from 42 to 65 years. There was also wide variability among subjects between and within the studies with regard to disease-free interval (the time between diagnosis of cancer and initiating ERT), duration of ERT use, and length of follow-up (Table). A few studies matched controls to ERT users based on these variables^16-18,24 or demonstrated that the groups were comparable.^19,21 In no study were subjects matched on type of treatment, race, estrogen receptor status, smoking, or other potentially important prognostic factors. Estrogen receptor status was unavailable for a large number of patients in these studies and could not be used for comparison.

Several studies contained methodologic flaws that resulted in important differences between comparison groups. Bluming and colleagues provided an unpublished analysis of recurrences in a sample of ERT users with previous T1N0 (stage I) cancers compared with a separate data set of similar patients who did not use ERT. In that study, tumor size was not known for 62% of the control group and 36% of the ERT group. Median follow-up was shorter in the ERT group, the tumors were smaller, the diagnoses were later, and patients were more likely to have received chemotherapy. Natrajan et al²⁰ compared 50 ERT users with 18 nonusers who left their clinic and were followed elsewhere. ERT users were younger than the nonusers and had longer follow-up. Little information was given regarding the cancer stages of the nonusers, and this was the only study primarily using hormone pellets and combining estrogen with testosterone in most patients. Habel et al²³ included only patients with ductal carcinoma in situ in a retrospective cohort study in which exposure was ascertained by mailed survey. Only 67% responded to the survey, and no baseline data comparing the ERT users with nonusers on important prognostic factors were provided. In a study by Beckman et al,²⁵ users were younger and less likely than nonusers to have grade 3 cancer (16% vs 30%), although this difference was reported to be nonsignificant. Median duration of follow-up was also longer in nonusers than in users (42 vs 37 months). In an unmatched study¹⁵ of ERT users and nonusers from the same practices in Australia, significant differences were found between groups in age, stage, and type of treatment rendered.

Because of the strong potential for bias due to baseline differences in risk of breast cancer recurrence, subanalyses included only those studies for which differences in important prognostic factors were not apparent.^16-19,21,24 In the case of the Australian study, a subset of the data, matched 2:1 on age, node status, tumor diameter, disease-free interval, and year of diagnosis, was found in an earlier report¹⁸ and used in the subanalysis.

Meta-analysis results

Overall, 8 studies reported the recurrence of breast cancer as an outcome. A meta-analysis of these studies showed that breast cancer survivors using ERT experienced no increase in the risk of recurrence compared with nonusers (8.2% vs 10.2%; RR, 0.72, 95% confidence interval [CI], 0.47–1.10). Because no statistical heterogeneity was demonstrated, a fixed effects model was used. Studies were analyzed separately depending on whether patients were matched or reportedly similar on factors such as age at diagnosis, tumor stage, and disease-free interval. Results were similar (Figure 1).

Six studies were included in a combined analysis of overall mortality (Figure 2). The ERT users in these studies experienced significantly fewer deaths (3.0%) than the nonusers (11.4%) over the combined study periods (RR, 0.18; 95% CI, 0.10–0.31; numbers needed to treat = 12). Subanalyses of those studies in which groups were comparable showed similar results (RR, 0.21; 95% CI, 0.10–0.46).

Despite the variability in study designs and subjects, all tests for heterogeneity were nonsignificant. In addition, funnel plots showed no evidence of publication bias (Figure W1, available on the JFP Web site: www.jfponline.com).

All studies, controlled or not, that reported data on control of menopausal symptoms reported significant benefit with ERT.^{2,7-9,11,19,25}

FIGURE 1
Graphic summary of studies on recurrence of breast cancer in ERT users vs nonusers

FIGURE 2
Graphic summary of studies of total mortality among users vs nonusers of estrogen replacement therapy

Discussion

This meta-analysis of observational studies in breast cancer survivors refutes the hypothesis that ERT increases the risk of breast cancer recurrence and suggests that it may in fact reduce all-cause mortality. However, conclusions drawn from observational studies can be seriously limited by potential sources of bias. For example, the studies likely had a bias by indication. That is, patients with more aggressive prognostic factors may not have been prescribed ERT, thereby making the treatment group likely to have represented a subgroup with a lower risk of recurrence than the general population used for comparison. However, several studies matched controls on important prognostic factors, and elimination of the unmatched study did not significantly affect study results. Similarly, in the absence of randomization, unmeasured confounders may have played a role. The treatment and control groups might have differed on other predictors of mortality that were not considered, such as in a healthy user effect in which subjects on ERT may have been more informed of its benefits and followed other, more healthy lifestyle behaviors than the comparison groups. They also may have been followed more closely by their physicians than the average breast cancer survivor.

In general, the subjects of the included studies over-represented patients with lower severity of disease than the general population of breast cancer survivors. Few studies included any subjects with a history of stage IV cancer (1 case with distant metastases), and several included patients with stage II or lower. Therefore, the results of this systematic review may be best generalized only to patients with lower stage disease. In addition, although subjects used ERT for as long as 32 years, the average duration of ERT use was shorter than 4 years in all but 1 study; longer follow-up is needed to truly assess the long-term effects of ERT in these high-risk patients. Available published studies also do not provide the detail needed to explore the potential contributions of estrogen receptor status or concomitant tamoxifen use.

Our finding of no significant difference in cancer recurrence associated with ERT use among patients with breast cancer is consistent with that of another recent meta-analysis.²⁶ Those researchers constructed expected control groups by using the average disease free interval before starting ERT, and known nodal status distribution from several single-arm cohort studies to calculate relative risks of recurrence for these studies. This method introduces additional bias and several assumptions that may not be warranted. For instance, risk of recurrence is much higher in the first few years after treatment for primary breast cancer. Therefore, the remarkable variability in the disease-free intervals and duration of follow-up among subjects within each of these studies make it very difficult to estimate expected recurrence rates without the detailed individual data from the original studies. Despite the “within-study” and “between-study” variabilities, the results of the individual studies are quite similar.

Observational studies, although limited, do not hold the ethical problems inherent to randomized controlled trials and are especially appropriate with a treatment as controversial as estrogen in breast cancer survivors. Available studies have produced findings contrary to conventional belief and to the theory that likens ERT to “fuel on the fire” in breast cancer. Such a theory has, until recently, made it seem unethical to justify a randomized controlled trial of ERT in these patients. However, data from some of these individual studies have provided enough support that enrollment for such trials have begun.²⁷ Previous studies of breast cancer risk with estrogen use have suggested that more than 10 years of treatment are required to see an increase in primary breast cancer,²⁸ so we may not have definitive evidence for some time. Meanwhile, there is no compelling evidence to support universal withholding of estrogen from well-informed women with symptomatic menopause, particularly among survivors of low-stage breast cancer.

Estrogen-containing hormone replacement therapy (ERT) after menopause has been implicated as a causal factor in the development of primary breast cancer.^1,2 Fearing cancer recurrence, most physicians do not offer ERT to postmenopausal women with a history of breast cancer. However, estrogen deficiency, which is especially common in women after chemotherapy, can be associated with severe symptoms, reduced quality of life, and increased risk of osteoporosis and possibly coronary artery disease. Although there are theoretical justifications to discourage the use of ERT by women at high risk for breast cancer, there is little objective evidence that hormone replacement increases the likelihood of breast cancer recurrence or of mortality among survivors of primary breast cancer. It is difficult for clinicians and patients to make rational decisions regarding ERT in these patients, given the paucity of studies and the difficulty of interpreting the few studies available.

Several observational studies have been published on the use of estrogen and/or combined estrogen–progesterone hormone replacement therapy in women who have had breast cancer. Many of these studies have reported single-institution series of outcomes among survivors who opted to take ERT for their menopausal symptoms. These studies tend to demonstrate rather unimpressive incidences of recurrence and mortality events. However, it is possible that such studies underestimate the risks because patients who are given ERT may represent a subgroup with a better prognosis than other patients (bias by indication). A smaller number of studies has used comparison groups and attempted to control for disease severity and other factors associated with recurrence.

We conducted a meta-analysis of studies comparing women who used ERT after the diagnosis of breast cancer with a control group of non-ERT users to determine whether ERT is associated with an increased risk of cancer recurrence or all-cause mortality among breast cancer survivors.

Methods

Search strategy

We identified relevant studies through independent literature searches of Medline (from 1966 to August 2001) and Cancerlit (from 1986 to August 2001) with the use of OVID software and the following search terms: estrogen replacement therapy, hormone replacement therapy, breast neoplasms, neoplasm recurrence, survivors. No language restriction was imposed. A careful review of titles and abstracts was done to identify relevant articles, and for these, the full articles were retrieved for review. Bibliographies of identified studies and review articles were examined for additional citations. Medline and Cancerlit databases were also searched by the names of authors of relevant studies to identify any missed articles. The authors of large studies and experts from our institution were asked to review the reference list for completeness and to suggest sources of unpublished data.

Inclusion criteria

Studies were considered for inclusion into the meta-analysis if they met the following criteria: (1) the population studied was women with a previous diagnosis of breast cancer, (2) the risk factor considered was the use of systemic estrogen or any combination hormone replacement therapy that included estrogen, (3) the outcome measured included the recurrence of breast cancer (whether a new or recurring primary cancer) and/or mortality, and (4) the study design was a randomized controlled trial or cohort study comparing women who used ERT after their breast cancer diagnosis with a concurrent, historical, or population-based control group of women who did not. Single-arm cohort studies were retrieved and summarized qualitatively but not included in the statistical analysis. If more than 1 publication was identified which reported the same data, the study with the most recent or complete data was selected for the analysis. We independently reviewed all studies for inclusion, and any differences were resolved through consensus.

Validity assessment

All included studies were assessed for validity by 2 independent reviewers, blinded to study results, for the following characteristics: (1) prospective data collection, (2) clear subject inclusion criteria, (3) reliability of exposure, (4) similarity between exposed and unexposed groups, (5) loss to follow-up, and (6) reliability of outcome assessment. When threats to study validity were identified, attempts were made to determine whether these threats were likely to significantly influence the results of the study and to estimate the direction of the influence of these threats on the resulting data. Because baseline differences between the study groups are such an important threat to the validity of these studies, the studies were graded as higher quality and lower quality based on whether significant differences in known prognostic factors existed.

Data management and analysis

A data extraction form was created to aid consistent recording of data from all studies, and both investigators extracted data independently. Any discrepancies in data interpretation or abstraction were resolved through consensus. Study characteristics and results for single-arm cohort studies were presented descriptively. For controlled studies, data were entered as dichotomous variables into Review Manager 4.1 software, as distributed by the Cochrane Collaboration. Summary relative risk (RR) estimates were calculated by using a fixed effects model (Mantel-Haenszel method) unless the results were found to be statistically heterogeneous (P < .1) through the use of a Q statistic, in which case the more conservative random effects model (DerSimonian-Laird method) was used. A subanalysis was performed based on the quality ratings, with a lower rating given to studies in which the exposed and unexposed groups differed significantly on important prognostic factors such as age, tumor stage, and time since diagnosis. Funnel plots were constructed to identify possible publication bias.

Results

Description of studies

The original search yielded 24 relevant reports, including 1 unpublished report (Bluming AZ, personal communication, 2000) with 2 separate studies. One of these and 12 published single-arm cohort studies^3-14 were excluded because they lacked a control group, but a summary of these studies can be found online (Table W1, available on the JFP Web site: www.jfponline.com). Twelve reports^15-25 met the inclusion criteria and provided data comparing the rates of recurrence or mortality among patients who used ERT after the diagnosis of breast cancer and users vs controls. Among these studies were 8 independent cohort studies from the published literature,^{15-17,20,21,23-25} one set of unpublished data from Bluming et al, and one 6-month pilot randomized controlled trial.¹⁹ One matched cohort study¹⁸ presented recurrence data for 90 patients and 180 controls who were later included in a larger, non-matched study reporting recurrence and mortality.¹⁵ Another small study²² reported only deaths from breast cancer from a data set included at least in part in another report¹⁶ and was therefore excluded. Overall, the included studies accounted for 717 subjects who used hormone replacement therapy at some time after their diagnosis of breast cancer compared with 2545 nonusers. Characteristics of included studies are summarized in the Table.

TABLE
Characteristics of included studies

Methodologic quality

The quality of the studies was variable. The only randomized controlled trial¹⁹ was a 6-month pilot study, after which the allocation code was broken and patients were free to choose whether to be on treatment. Of the cohort studies, only 1 trial²¹ began with an inception cohort that combined data from 62 patients who elected to be part of a randomized controlled trial with that from another 257 who declined to be randomized but chose on their own whether to take ERT.²¹ One study was clearly retrospective²³ ; patients with ductal carcinoma in situ were identified through a cancer registry, and their exposures and recurrences were determined through a mailed questionnaire. The remaining studies used clinic records to identify patients who had been prescribed ERT and compared those recurrence and mortality rates with those of a control group comprising the remaining clinic patients^{15,18,20,24,25} or matched subjects selected from a regional cancer surveillance database.^15,16 Although the matching process controlled for some important prognostic factors (age, stage, and time since diagnosis), post-diagnosis ERT use was not recorded in the surveillance database, so these control groups may have contained patients who took ERT at some time, thereby diluting any differences that might be observed. Conversely, none of the cohort studies reported means confirming that those for whom HRT had been prescribed actually took it regularly.

Across all studies, the studied interventions included a systemic estrogen, usually in combination with progesterone unless the subject had had a hysterectomy. The mean age at diagnosis of cancer varied among studies, from 42 to 65 years. There was also wide variability among subjects between and within the studies with regard to disease-free interval (the time between diagnosis of cancer and initiating ERT), duration of ERT use, and length of follow-up (Table). A few studies matched controls to ERT users based on these variables^16-18,24 or demonstrated that the groups were comparable.^19,21 In no study were subjects matched on type of treatment, race, estrogen receptor status, smoking, or other potentially important prognostic factors. Estrogen receptor status was unavailable for a large number of patients in these studies and could not be used for comparison.

Several studies contained methodologic flaws that resulted in important differences between comparison groups. Bluming and colleagues provided an unpublished analysis of recurrences in a sample of ERT users with previous T1N0 (stage I) cancers compared with a separate data set of similar patients who did not use ERT. In that study, tumor size was not known for 62% of the control group and 36% of the ERT group. Median follow-up was shorter in the ERT group, the tumors were smaller, the diagnoses were later, and patients were more likely to have received chemotherapy. Natrajan et al²⁰ compared 50 ERT users with 18 nonusers who left their clinic and were followed elsewhere. ERT users were younger than the nonusers and had longer follow-up. Little information was given regarding the cancer stages of the nonusers, and this was the only study primarily using hormone pellets and combining estrogen with testosterone in most patients. Habel et al²³ included only patients with ductal carcinoma in situ in a retrospective cohort study in which exposure was ascertained by mailed survey. Only 67% responded to the survey, and no baseline data comparing the ERT users with nonusers on important prognostic factors were provided. In a study by Beckman et al,²⁵ users were younger and less likely than nonusers to have grade 3 cancer (16% vs 30%), although this difference was reported to be nonsignificant. Median duration of follow-up was also longer in nonusers than in users (42 vs 37 months). In an unmatched study¹⁵ of ERT users and nonusers from the same practices in Australia, significant differences were found between groups in age, stage, and type of treatment rendered.

Because of the strong potential for bias due to baseline differences in risk of breast cancer recurrence, subanalyses included only those studies for which differences in important prognostic factors were not apparent.^16-19,21,24 In the case of the Australian study, a subset of the data, matched 2:1 on age, node status, tumor diameter, disease-free interval, and year of diagnosis, was found in an earlier report¹⁸ and used in the subanalysis.

Meta-analysis results

Overall, 8 studies reported the recurrence of breast cancer as an outcome. A meta-analysis of these studies showed that breast cancer survivors using ERT experienced no increase in the risk of recurrence compared with nonusers (8.2% vs 10.2%; RR, 0.72, 95% confidence interval [CI], 0.47–1.10). Because no statistical heterogeneity was demonstrated, a fixed effects model was used. Studies were analyzed separately depending on whether patients were matched or reportedly similar on factors such as age at diagnosis, tumor stage, and disease-free interval. Results were similar (Figure 1).

Six studies were included in a combined analysis of overall mortality (Figure 2). The ERT users in these studies experienced significantly fewer deaths (3.0%) than the nonusers (11.4%) over the combined study periods (RR, 0.18; 95% CI, 0.10–0.31; numbers needed to treat = 12). Subanalyses of those studies in which groups were comparable showed similar results (RR, 0.21; 95% CI, 0.10–0.46).

Despite the variability in study designs and subjects, all tests for heterogeneity were nonsignificant. In addition, funnel plots showed no evidence of publication bias (Figure W1, available on the JFP Web site: www.jfponline.com).

All studies, controlled or not, that reported data on control of menopausal symptoms reported significant benefit with ERT.^{2,7-9,11,19,25}

FIGURE 1
Graphic summary of studies on recurrence of breast cancer in ERT users vs nonusers

FIGURE 2
Graphic summary of studies of total mortality among users vs nonusers of estrogen replacement therapy

Discussion

This meta-analysis of observational studies in breast cancer survivors refutes the hypothesis that ERT increases the risk of breast cancer recurrence and suggests that it may in fact reduce all-cause mortality. However, conclusions drawn from observational studies can be seriously limited by potential sources of bias. For example, the studies likely had a bias by indication. That is, patients with more aggressive prognostic factors may not have been prescribed ERT, thereby making the treatment group likely to have represented a subgroup with a lower risk of recurrence than the general population used for comparison. However, several studies matched controls on important prognostic factors, and elimination of the unmatched study did not significantly affect study results. Similarly, in the absence of randomization, unmeasured confounders may have played a role. The treatment and control groups might have differed on other predictors of mortality that were not considered, such as in a healthy user effect in which subjects on ERT may have been more informed of its benefits and followed other, more healthy lifestyle behaviors than the comparison groups. They also may have been followed more closely by their physicians than the average breast cancer survivor.

In general, the subjects of the included studies over-represented patients with lower severity of disease than the general population of breast cancer survivors. Few studies included any subjects with a history of stage IV cancer (1 case with distant metastases), and several included patients with stage II or lower. Therefore, the results of this systematic review may be best generalized only to patients with lower stage disease. In addition, although subjects used ERT for as long as 32 years, the average duration of ERT use was shorter than 4 years in all but 1 study; longer follow-up is needed to truly assess the long-term effects of ERT in these high-risk patients. Available published studies also do not provide the detail needed to explore the potential contributions of estrogen receptor status or concomitant tamoxifen use.

Our finding of no significant difference in cancer recurrence associated with ERT use among patients with breast cancer is consistent with that of another recent meta-analysis.²⁶ Those researchers constructed expected control groups by using the average disease free interval before starting ERT, and known nodal status distribution from several single-arm cohort studies to calculate relative risks of recurrence for these studies. This method introduces additional bias and several assumptions that may not be warranted. For instance, risk of recurrence is much higher in the first few years after treatment for primary breast cancer. Therefore, the remarkable variability in the disease-free intervals and duration of follow-up among subjects within each of these studies make it very difficult to estimate expected recurrence rates without the detailed individual data from the original studies. Despite the “within-study” and “between-study” variabilities, the results of the individual studies are quite similar.

Observational studies, although limited, do not hold the ethical problems inherent to randomized controlled trials and are especially appropriate with a treatment as controversial as estrogen in breast cancer survivors. Available studies have produced findings contrary to conventional belief and to the theory that likens ERT to “fuel on the fire” in breast cancer. Such a theory has, until recently, made it seem unethical to justify a randomized controlled trial of ERT in these patients. However, data from some of these individual studies have provided enough support that enrollment for such trials have begun.²⁷ Previous studies of breast cancer risk with estrogen use have suggested that more than 10 years of treatment are required to see an increase in primary breast cancer,²⁸ so we may not have definitive evidence for some time. Meanwhile, there is no compelling evidence to support universal withholding of estrogen from well-informed women with symptomatic menopause, particularly among survivors of low-stage breast cancer.

Sinusitis is a common clinical problem with significant morbidity and often refractory symptoms that accounted for approximately 26.7 million office and emergency visits and resulted in $5.8 billion spent in direct costs in 1996.¹ Sinusitis was the fifth most common diagnosis for which antibiotics were prescribed from 1985 to 1992.² In 1992, 13 million prescriptions were written for sinusitis, up from 5.8 million in 1985.² The number of US chronic sinusitis cases in 1994 was estimated at 35 million, for a prevalence of 134 per 1000 patients.³ The effect of sinusitis on patients’ quality of life (QOL) is significant and can rate as high as back pain, congestive heart disease, and chronic obstructive pulmonary disease on some measures.⁴

Hypertonic nasal irrigation is a therapy that flushes the nasal cavity with saline solution, facilitating a wash of the structures within. Originally part of the Yogic tradition, this technique is anecdotally regarded as safe and effective; it has been suggested as adjunctive therapy for sinusitis and sinus symptoms.^5-7 Potential efficacy is supported by the observation that hypertonic saline improves mucociliary clearance,⁸ thins mucus,^9,10 and may decrease inflammation.⁸ Optimal irrigant salinity and pH are unclear.^10,11 Several small trials examining nasal irrigation have suggested that nasal irrigation is safe, improves nasal symptoms, and is physically tolerable, but inclusion criteria, intervention protocols, and methodological quality vary.^12-18 Improvement of QOL scores^12-14 and several surrogate measures^14-16 have been reported. No study has rigorously evaluated nasal irrigation over a longer period for its effect on QOL, antibiotic and nasal medication use, symptom severity, compliance, and side effects.

We conducted a randomized controlled trial to test the hypotheses that daily hypertonic saline nasal irrigation improves symptoms, decreases antibiotic and nasal medication use, and improves QOL in adult subjects with a history of sinusitis.

Methods

The study protocol was approved by the University of Wisconsin Health Sciences Human Subjects Committee. Subjects were enrolled from May to August 2000 and, after a study period of 6 months, were exited from November 2000 to February 2001. No prior studies existed at inception to guide sample size estimation. Power calculations performed before study initiation indicated that a sample size of 60 subjects would provide 80% power to detect a 10% difference in the Rhinosinusitis Disability Index (RSDI) between study groups. Due to the high patient burden of this study, we assumed a 25% dropout rate.

Randomization

The randomization scheme was prepared by the Investigational Drug Services of the University of Wisconsin Hospital and Clinics. Subjects were stratified by smoking status and then randomized by using an approximate 2:1 block design, with 10 subjects per block. Therefore 68% of subjects were assigned to the experimental group and 32% to the control group. A 2:1 scheme favoring the experimental group was selected due to resource limitations.

Eligibility criteria and subject recruitment

The recruitment and subject participation scheme is shown in Figure W1 (available on the JFP Web site: http://www.jfponline.com). The billing databases for the University of Wisconsin primary care and Ear, Nose, and Throat (ENT) practices were screened for acute and chronic sinusitis (codes 461 and 473, respectively, from the International Classification of Diseases, Ninth Revision). Patients 18 to 65 years old with 2 episodes of acute sinusitis or 1 episode of chronic sinusitis per year for 2 consecutive years (n = 602) were sent a letter explaining the study and inviting participation, along with an opt-out postcard. If no card was returned, potential subjects were phoned. Exclusion criteria included pregnancy and comorbidity significant enough to preclude travel to an informational meeting or performance of the nasal irrigation technique. Patients indicating “moderate to severe” impact of sinus symptoms on their QOL on a Likert scale of 1 to 7 were invited to attend an informational meeting involving enrollment, randomization, and training (n = 128). Of those potential subjects, 44 declined the meeting or were ineligible; 84 agreed to attend the meeting, 77 attended, and 76 enrolled. Of the initial group of 602 potential subjects, 375 were not contacted because the study census reached intended sample size.

One of us (D.R., R.M., or A.Z.) facilitated each informational meeting of 1 to 6 persons. Sealed envelopes containing the patient’s randomized group assignment were distributed to subjects in the order they entered the room. The group assignment was unknown to the investigator. Subjects broke the seal and learned their assignment. Thereafter, investigators were not blind to subjects’ group assignment. Persons managing and analyzing data also saw unblinded data but had no contact with subjects. Participants heard a brief presentation about sinus disease and its treatment. Nasal irrigation theory and technique were explained. Seventy-six subjects consented and were allocated by their randomized group assignments to experimental (n = 52) or control (n = 24) groups. Control subjects continued treatment of sinus disease in their usual manner. Experimental subjects saw a brief demonstration film, witnessed nasal irrigation by the facilitator, and demonstrated proficiency with the nasal irrigation technique before departure. Subjects were provided all ingredients and materials for 6 months of daily nasal irrigation. Experimental subjects also continued usual care for sinus disease.

Intervention

Subjects in the experimental group were asked to irrigate the nose (150 mL through each nostril) daily for 6 months with the SinuCleanse¹⁹ nasal cup containing 2.0% saline buffered with baking soda (1 heaping teaspoon of canning salt, one half teaspoon of baking soda, and 1 pint of tap water; (Table 1). Solution was mixed fresh every 1 to 2 days. All subjects were phoned at 2 weeks to assess initial compliance with study protocols and thereafter if assessment instruments were not returned promptly.

TABLE 1
Baseline patient characteristics*

Outcome measures

The primary outcomes were QOL scores from 2 validated questionnaires: the general health assessment Medical Outcomes Survey Short Form (SF-12)²⁰ and the RSDI,²¹ a disease-specific instrument assessing QOL in emotional, functional, and physical domains. We reworded the phrase my problem to my sinus symptoms on several RSDI items. Consensus within the research group and among consulted experts was that this minor change facilitated more accurate reading and reporting. We also measured overall sinus symptom severity with a Single-Item Symptom Severity Assessment (SIA): “Please evaluate the overall severity of your sinus symptoms since you enrolled in the study”; higher scores on the Likert scale SIA indicated increased severity. Scales for RSDI and SF-12 ranged from 0 to 100 points, with higher scores indicating better overall QOL. Each was completed at baseline and at 1.5, 3, and 6 months; at the 6-month assessment, subjects were shown their baseline answers for comparison because they had told us they needed to recall answers to past questions. They believed they knew whether they felt better or worse and wanted their later answers to reflect this change. Allowing subjects to view previous scores is an accepted research practice.²² However, because we did not allow subjects to see their baseline answers at 1.5 and 3 months, scores must be interpreted in light of the availability of the baseline data to the subjects.

Secondary outcomes were assessed with multiple methods. Compliance with nasal irrigation was recorded in a daily diary. The presence or absence of sinus symptoms (headache, congestion, facial pressure, facial pain, nasal discharge), antibiotic use, and nasal-spray use was assessed every 2 weeks. An exit questionnaire asked subjects to report categorically whether their sinus-related QOL had gotten worse, stayed the same, or improved, and to estimate the percentage of change (scale from 0 to ±100%). Overall satisfaction and side effects were reported at 6 months.

Statistical methods

Baseline characteristics of experimental and control groups were compared to assess randomization. Analysis, performed on an intention-to-treat basis, involved all 76 subjects randomized into the study. As dictated by the intention-to-treat model, the few missing values were imputed with multiple regression. Repeated measures analysis of variance contrasted the primary outcomes, that is, QOL status and sinus symptom scores within each group at baseline and subsequent periods. Differences between experimental and control groups were analyzed at each point in the repeated measures model and comprehensively for the entire time frame of the study. Statistical significance was assessed with 2-tailed tests. Data are presented as mean values with range of standard error, unless otherwise indicated.

Results

The study sample (Table 1) consisted of 76 subjects (55 female) randomized to experimental (n = 52) and control (n = 24) groups. Subjects’ ages ranged from 19 to 62 years, with a mean age of 42 years. Sixty-nine subjects (46 experimental and 23 control) completed the study. Seven subjects dropped out of the study at 1.5 months or earlier. A phone questionnaire was completed by 3 experimental dropouts; 2 of the 3 identified “lack of time” as the main reason for leaving the study; the remaining subject did not specify a reason. All 3 identified nasal irrigation as “helpful,” and none identified side effects as significant. The remaining 4 subjects were lost to follow-up. Dropouts tended to have slightly better baseline RSDI scores than nondropouts, 66.8 vs 58.1 points, but this difference was not significant (P = .15). No significant baseline differences were found between the groups of mostly white, female, well-educated subjects (Table 1). Baseline RSDI, SF-12, and SIA scores were similar in both groups. Although ENT subjects tended to have slightly worse baseline RSDI and SIA scores and improved slightly more during the study than other experimental subjects, the effect of clinic type (ENT vs primary care) was not statistically significant. By chance all subjects from ENT clinics (n = 6) and a disproportionate percentage of subjects with chronic sinusitis were randomized to the experimental group. Neither variable was statistically significant.

Experimental subjects showed a significant improvement in RSDI scores: 58.4 ± 2.0, 66.6 ± 2.2, 72.4 ± 2.2, and 72.8 ± 2.2 points at baseline, 1.5, 3, and 6 months, respectively (Table 2, Figure 2). Although the difference was not significant (P = .08), experimental subjects whose initial RSDI score was less than 50 points improved the most, with an average score change of 17.8 ± 4.4, and comparable control subjects had an average RSDI score change of 8.8 ± 2.9 points. Emotional and functional RSDI domains were not significantly related to score change; however, the physical domain of the survey was significant (P = .05).

SIA scores for experimental subjects improved (P < .05) at all follow-up points compared with control subjects; scores for the experimental group were 3.9 ± 0.1, 3.1 ± 0.2, 2.7 ± 0.2, and 2.4 ± 0.1 points at baseline, 1.5, 3, and 6 months, respectively (Table 2, Figure 2).

SF-12 score showed no significant differences between groups at any follow-up point but by 6 months trended toward significance (P = .06; Table 2).

Forty-one (93%) experimental subjects completing the exit questionnaire reported improvement. Most (n = 16, 73%) control subjects reported no change, but 18% reported worsening (P < .001; Table 3). Experimental subjects reported an average of 57 ± 4.5% improvement (range, 0–100%), whereas control subjects reported an average of 7 ± 5.9% worsening (range, -80% to 50%; P < .001).

Experimental subjects reported using nasal irrigation on 87% of days during the study; 31 subjects reported using nasal irrigation on 91% or more days, 13 subjects on 76% to 90% of days, and 5 subjects on 51% to 75% of days. Only 3 subjects used nasal irrigation on 50% or fewer days; these 3 subjects had relatively good baseline RSDI and SIA scores compared with other experimental subjects. Compliance was not significantly associated with changes in SIA or RSDI scores. The average survey completion rate was 96% at each assessment by each group.

Experimental subjects spent fewer 2-week blocks with nasal congestion, sinus headache, and frontal pain and pressure and used antibiotics and nasal sprays in fewer blocks (Table 3).

Forty-four experimental subjects answered questions about satisfaction and side effects. Forty-two stated they “will continue to use” nasal irrigation; the remaining 2 subjects found nasal irrigation less helpful but did not experience side effects. All 44 subjects “would recommend” nasal irrigation to friends or family with sinus problems. Ten subjects (23%) experienced side effects; 8 identified nasal irritation, nasal burning, tearing, nosebleeds, headache, or nasal drainage as occurring but “not significant.” Two subjects identified nasal burning, irritation, and headache as “significant,” but this did not change their high satisfaction rating. Of the 10 subjects who experienced side effects, 4 reduced or eliminated the side effects by temporarily alternating treatment days or decreasing salinity by 50%.

TABLE 2
Primary outcomes: RSDI, SF-12, and SIA baseline scores and mean score changes*

TABLE 3
Secondary outcomes

FIGURE 1
Position of nasal cup for nasal irrigation therapy A B

FIGURE 2
Mean RSDI and SIA scores in control and experimental subjects

DISCUSSION

Our trial of daily hypertonic nasal irrigation produced several significant findings. We found consistent, statistically significant improvements in QOL (RSDI) and overall symptom severity (SIA). This was consistent with QOL improvement previously reported over short periods with the use of disease-specific measures.^12-14 The RSDI is a moderately well-developed and validated disease-specific QOL instrument.^21-23 The “minimal clinically important difference,” defined as the average score improvement needed to justify costs and risks,^24-26 has not been established for sinusitis. However, it has been estimated for other disease states. For example, a half-point change on a 7-point Likert scale corresponds to estimates of important change in patients with chronic heart and lung disease.^22,27 Others have found similar relationships.^28-31 In our study, RSDI scores among treated subjects averaged 6.0 and 15.5 points better than controls at 3 and 6 months, respectively. On the SIA, treated subjects averaged 0.6, 0.9, and 1.6 points better. Extrapolating from these findings, these differences appear to be clinically significant. By using 10% improvement of the RSDI, our data showed numbers needed to treat of 9, 5, and 2 at 1.5, 3, and 6 months, respectively (95% confidence interval at 6 months, 1.4–2.6). Numbers needed to treat for SIA, symptom frequency, and medication use were similar. SF-12 improvement, although not statistically significant in this small trial, may represent clinically significant improvements in general health-related QOL.

“Percentage change” is used often by clinicians to gauge therapeutic progress. Ours is the first study to document such change in sinusitis patients using nasal irrigation. Ours is also the first trial to show decreased symptom frequency over a 6-month period. Shorter trials have documented improvement in patients with nasal symptoms^12,13,17,18 or with chronic sinusitis in adult^14,15 and pediatric¹⁶ populations. Consistent with improved symptoms and QOL, experimental subjects decreased their use of antibiotics and nasal sprays, as previously reported in a short trial.¹²

Side effects have not been carefully assessed in previous trials. Although generally safe, daily hypertonic nasal irrigation was associated with some clinically minor side effects. Interestingly, subjects were able to decrease side effects by adjusting irrigation schedule or salinity. Side effects were not sufficiently bothersome to stop therapy. Compliance with daily therapy was very high and is previously unreported. Although this was consistent with a positive effect on relatively severe symptoms, we believe high compliance also was related to teaching, demonstrated proficiency with nasal irrigation, and close telephone follow-up. One prior study reported subjects’ observation of the first nasal irrigation¹⁵; several studies reported providing some education.^1214,18

Our study has several limitations. It was not blinded or placebo controlled. Blinding subjects to a physical therapy is inherently difficult. Investigators who have tried to use normal saline placebos probably affected outcomes.^14-16 One trial using a fresh water (0% saline) placebo was stopped early when several control subjects developed otitis media.³² The investigators also were unblinded, possibly creating observer bias.

Methodologic and recruitment strengths of this study included effective randomization, matched control group, intention-to-treat analysis, low missing data rates, high compliance rate, and low dropout rate. Clinical strengths included significant findings on most parameters assessed. Particularly intriguing was the decreased use of antibiotics in the experimental group. This study offered strong evidence that nasal irrigation is a safe, effective, and inexpensive (nasal pot, $15; daily therapy, <$1/month) therapy for sinus disease that properly trained patients will use. Although questions about the protocol (schedule, concentration, and buffering) and indications require further study in a more diverse patient population, clinicians may confidently recommend nasal irrigation; it offers significant hope for symptomatic relief and QOL improvement for millions of individuals with sinus disease who often have few therapeutic options.

CONCLUSIONS

Daily hypertonic saline nasal irrigation improves sinus-related QOL, decreases symptoms, and decreases medication use in patients with frequent sinusitis. Primary care physicians can feel comfortable recommending this therapy.

Acknowledgments

We thank Thomas Pasic, MD, Michael McDonald, MD, and Diane Heatley, MD, Department of Otolaryngology, University of Wisconsin, Madison.

Sinusitis is a common clinical problem with significant morbidity and often refractory symptoms that accounted for approximately 26.7 million office and emergency visits and resulted in $5.8 billion spent in direct costs in 1996.¹ Sinusitis was the fifth most common diagnosis for which antibiotics were prescribed from 1985 to 1992.² In 1992, 13 million prescriptions were written for sinusitis, up from 5.8 million in 1985.² The number of US chronic sinusitis cases in 1994 was estimated at 35 million, for a prevalence of 134 per 1000 patients.³ The effect of sinusitis on patients’ quality of life (QOL) is significant and can rate as high as back pain, congestive heart disease, and chronic obstructive pulmonary disease on some measures.⁴

Hypertonic nasal irrigation is a therapy that flushes the nasal cavity with saline solution, facilitating a wash of the structures within. Originally part of the Yogic tradition, this technique is anecdotally regarded as safe and effective; it has been suggested as adjunctive therapy for sinusitis and sinus symptoms.^5-7 Potential efficacy is supported by the observation that hypertonic saline improves mucociliary clearance,⁸ thins mucus,^9,10 and may decrease inflammation.⁸ Optimal irrigant salinity and pH are unclear.^10,11 Several small trials examining nasal irrigation have suggested that nasal irrigation is safe, improves nasal symptoms, and is physically tolerable, but inclusion criteria, intervention protocols, and methodological quality vary.^12-18 Improvement of QOL scores^12-14 and several surrogate measures^14-16 have been reported. No study has rigorously evaluated nasal irrigation over a longer period for its effect on QOL, antibiotic and nasal medication use, symptom severity, compliance, and side effects.

We conducted a randomized controlled trial to test the hypotheses that daily hypertonic saline nasal irrigation improves symptoms, decreases antibiotic and nasal medication use, and improves QOL in adult subjects with a history of sinusitis.

Methods

The study protocol was approved by the University of Wisconsin Health Sciences Human Subjects Committee. Subjects were enrolled from May to August 2000 and, after a study period of 6 months, were exited from November 2000 to February 2001. No prior studies existed at inception to guide sample size estimation. Power calculations performed before study initiation indicated that a sample size of 60 subjects would provide 80% power to detect a 10% difference in the Rhinosinusitis Disability Index (RSDI) between study groups. Due to the high patient burden of this study, we assumed a 25% dropout rate.

Randomization

The randomization scheme was prepared by the Investigational Drug Services of the University of Wisconsin Hospital and Clinics. Subjects were stratified by smoking status and then randomized by using an approximate 2:1 block design, with 10 subjects per block. Therefore 68% of subjects were assigned to the experimental group and 32% to the control group. A 2:1 scheme favoring the experimental group was selected due to resource limitations.

Eligibility criteria and subject recruitment

The recruitment and subject participation scheme is shown in Figure W1 (available on the JFP Web site: http://www.jfponline.com). The billing databases for the University of Wisconsin primary care and Ear, Nose, and Throat (ENT) practices were screened for acute and chronic sinusitis (codes 461 and 473, respectively, from the International Classification of Diseases, Ninth Revision). Patients 18 to 65 years old with 2 episodes of acute sinusitis or 1 episode of chronic sinusitis per year for 2 consecutive years (n = 602) were sent a letter explaining the study and inviting participation, along with an opt-out postcard. If no card was returned, potential subjects were phoned. Exclusion criteria included pregnancy and comorbidity significant enough to preclude travel to an informational meeting or performance of the nasal irrigation technique. Patients indicating “moderate to severe” impact of sinus symptoms on their QOL on a Likert scale of 1 to 7 were invited to attend an informational meeting involving enrollment, randomization, and training (n = 128). Of those potential subjects, 44 declined the meeting or were ineligible; 84 agreed to attend the meeting, 77 attended, and 76 enrolled. Of the initial group of 602 potential subjects, 375 were not contacted because the study census reached intended sample size.

One of us (D.R., R.M., or A.Z.) facilitated each informational meeting of 1 to 6 persons. Sealed envelopes containing the patient’s randomized group assignment were distributed to subjects in the order they entered the room. The group assignment was unknown to the investigator. Subjects broke the seal and learned their assignment. Thereafter, investigators were not blind to subjects’ group assignment. Persons managing and analyzing data also saw unblinded data but had no contact with subjects. Participants heard a brief presentation about sinus disease and its treatment. Nasal irrigation theory and technique were explained. Seventy-six subjects consented and were allocated by their randomized group assignments to experimental (n = 52) or control (n = 24) groups. Control subjects continued treatment of sinus disease in their usual manner. Experimental subjects saw a brief demonstration film, witnessed nasal irrigation by the facilitator, and demonstrated proficiency with the nasal irrigation technique before departure. Subjects were provided all ingredients and materials for 6 months of daily nasal irrigation. Experimental subjects also continued usual care for sinus disease.

Intervention

Subjects in the experimental group were asked to irrigate the nose (150 mL through each nostril) daily for 6 months with the SinuCleanse¹⁹ nasal cup containing 2.0% saline buffered with baking soda (1 heaping teaspoon of canning salt, one half teaspoon of baking soda, and 1 pint of tap water; (Table 1). Solution was mixed fresh every 1 to 2 days. All subjects were phoned at 2 weeks to assess initial compliance with study protocols and thereafter if assessment instruments were not returned promptly.

TABLE 1
Baseline patient characteristics*

Outcome measures

The primary outcomes were QOL scores from 2 validated questionnaires: the general health assessment Medical Outcomes Survey Short Form (SF-12)²⁰ and the RSDI,²¹ a disease-specific instrument assessing QOL in emotional, functional, and physical domains. We reworded the phrase my problem to my sinus symptoms on several RSDI items. Consensus within the research group and among consulted experts was that this minor change facilitated more accurate reading and reporting. We also measured overall sinus symptom severity with a Single-Item Symptom Severity Assessment (SIA): “Please evaluate the overall severity of your sinus symptoms since you enrolled in the study”; higher scores on the Likert scale SIA indicated increased severity. Scales for RSDI and SF-12 ranged from 0 to 100 points, with higher scores indicating better overall QOL. Each was completed at baseline and at 1.5, 3, and 6 months; at the 6-month assessment, subjects were shown their baseline answers for comparison because they had told us they needed to recall answers to past questions. They believed they knew whether they felt better or worse and wanted their later answers to reflect this change. Allowing subjects to view previous scores is an accepted research practice.²² However, because we did not allow subjects to see their baseline answers at 1.5 and 3 months, scores must be interpreted in light of the availability of the baseline data to the subjects.

Secondary outcomes were assessed with multiple methods. Compliance with nasal irrigation was recorded in a daily diary. The presence or absence of sinus symptoms (headache, congestion, facial pressure, facial pain, nasal discharge), antibiotic use, and nasal-spray use was assessed every 2 weeks. An exit questionnaire asked subjects to report categorically whether their sinus-related QOL had gotten worse, stayed the same, or improved, and to estimate the percentage of change (scale from 0 to ±100%). Overall satisfaction and side effects were reported at 6 months.

Statistical methods

Baseline characteristics of experimental and control groups were compared to assess randomization. Analysis, performed on an intention-to-treat basis, involved all 76 subjects randomized into the study. As dictated by the intention-to-treat model, the few missing values were imputed with multiple regression. Repeated measures analysis of variance contrasted the primary outcomes, that is, QOL status and sinus symptom scores within each group at baseline and subsequent periods. Differences between experimental and control groups were analyzed at each point in the repeated measures model and comprehensively for the entire time frame of the study. Statistical significance was assessed with 2-tailed tests. Data are presented as mean values with range of standard error, unless otherwise indicated.

Results

The study sample (Table 1) consisted of 76 subjects (55 female) randomized to experimental (n = 52) and control (n = 24) groups. Subjects’ ages ranged from 19 to 62 years, with a mean age of 42 years. Sixty-nine subjects (46 experimental and 23 control) completed the study. Seven subjects dropped out of the study at 1.5 months or earlier. A phone questionnaire was completed by 3 experimental dropouts; 2 of the 3 identified “lack of time” as the main reason for leaving the study; the remaining subject did not specify a reason. All 3 identified nasal irrigation as “helpful,” and none identified side effects as significant. The remaining 4 subjects were lost to follow-up. Dropouts tended to have slightly better baseline RSDI scores than nondropouts, 66.8 vs 58.1 points, but this difference was not significant (P = .15). No significant baseline differences were found between the groups of mostly white, female, well-educated subjects (Table 1). Baseline RSDI, SF-12, and SIA scores were similar in both groups. Although ENT subjects tended to have slightly worse baseline RSDI and SIA scores and improved slightly more during the study than other experimental subjects, the effect of clinic type (ENT vs primary care) was not statistically significant. By chance all subjects from ENT clinics (n = 6) and a disproportionate percentage of subjects with chronic sinusitis were randomized to the experimental group. Neither variable was statistically significant.

Experimental subjects showed a significant improvement in RSDI scores: 58.4 ± 2.0, 66.6 ± 2.2, 72.4 ± 2.2, and 72.8 ± 2.2 points at baseline, 1.5, 3, and 6 months, respectively (Table 2, Figure 2). Although the difference was not significant (P = .08), experimental subjects whose initial RSDI score was less than 50 points improved the most, with an average score change of 17.8 ± 4.4, and comparable control subjects had an average RSDI score change of 8.8 ± 2.9 points. Emotional and functional RSDI domains were not significantly related to score change; however, the physical domain of the survey was significant (P = .05).

SIA scores for experimental subjects improved (P < .05) at all follow-up points compared with control subjects; scores for the experimental group were 3.9 ± 0.1, 3.1 ± 0.2, 2.7 ± 0.2, and 2.4 ± 0.1 points at baseline, 1.5, 3, and 6 months, respectively (Table 2, Figure 2).

SF-12 score showed no significant differences between groups at any follow-up point but by 6 months trended toward significance (P = .06; Table 2).

Forty-one (93%) experimental subjects completing the exit questionnaire reported improvement. Most (n = 16, 73%) control subjects reported no change, but 18% reported worsening (P < .001; Table 3). Experimental subjects reported an average of 57 ± 4.5% improvement (range, 0–100%), whereas control subjects reported an average of 7 ± 5.9% worsening (range, -80% to 50%; P < .001).

Experimental subjects reported using nasal irrigation on 87% of days during the study; 31 subjects reported using nasal irrigation on 91% or more days, 13 subjects on 76% to 90% of days, and 5 subjects on 51% to 75% of days. Only 3 subjects used nasal irrigation on 50% or fewer days; these 3 subjects had relatively good baseline RSDI and SIA scores compared with other experimental subjects. Compliance was not significantly associated with changes in SIA or RSDI scores. The average survey completion rate was 96% at each assessment by each group.

Experimental subjects spent fewer 2-week blocks with nasal congestion, sinus headache, and frontal pain and pressure and used antibiotics and nasal sprays in fewer blocks (Table 3).

Forty-four experimental subjects answered questions about satisfaction and side effects. Forty-two stated they “will continue to use” nasal irrigation; the remaining 2 subjects found nasal irrigation less helpful but did not experience side effects. All 44 subjects “would recommend” nasal irrigation to friends or family with sinus problems. Ten subjects (23%) experienced side effects; 8 identified nasal irritation, nasal burning, tearing, nosebleeds, headache, or nasal drainage as occurring but “not significant.” Two subjects identified nasal burning, irritation, and headache as “significant,” but this did not change their high satisfaction rating. Of the 10 subjects who experienced side effects, 4 reduced or eliminated the side effects by temporarily alternating treatment days or decreasing salinity by 50%.

TABLE 2
Primary outcomes: RSDI, SF-12, and SIA baseline scores and mean score changes*

TABLE 3
Secondary outcomes

FIGURE 1
Position of nasal cup for nasal irrigation therapy A B

FIGURE 2
Mean RSDI and SIA scores in control and experimental subjects

DISCUSSION

Our trial of daily hypertonic nasal irrigation produced several significant findings. We found consistent, statistically significant improvements in QOL (RSDI) and overall symptom severity (SIA). This was consistent with QOL improvement previously reported over short periods with the use of disease-specific measures.^12-14 The RSDI is a moderately well-developed and validated disease-specific QOL instrument.^21-23 The “minimal clinically important difference,” defined as the average score improvement needed to justify costs and risks,^24-26 has not been established for sinusitis. However, it has been estimated for other disease states. For example, a half-point change on a 7-point Likert scale corresponds to estimates of important change in patients with chronic heart and lung disease.^22,27 Others have found similar relationships.^28-31 In our study, RSDI scores among treated subjects averaged 6.0 and 15.5 points better than controls at 3 and 6 months, respectively. On the SIA, treated subjects averaged 0.6, 0.9, and 1.6 points better. Extrapolating from these findings, these differences appear to be clinically significant. By using 10% improvement of the RSDI, our data showed numbers needed to treat of 9, 5, and 2 at 1.5, 3, and 6 months, respectively (95% confidence interval at 6 months, 1.4–2.6). Numbers needed to treat for SIA, symptom frequency, and medication use were similar. SF-12 improvement, although not statistically significant in this small trial, may represent clinically significant improvements in general health-related QOL.

“Percentage change” is used often by clinicians to gauge therapeutic progress. Ours is the first study to document such change in sinusitis patients using nasal irrigation. Ours is also the first trial to show decreased symptom frequency over a 6-month period. Shorter trials have documented improvement in patients with nasal symptoms^12,13,17,18 or with chronic sinusitis in adult^14,15 and pediatric¹⁶ populations. Consistent with improved symptoms and QOL, experimental subjects decreased their use of antibiotics and nasal sprays, as previously reported in a short trial.¹²

Side effects have not been carefully assessed in previous trials. Although generally safe, daily hypertonic nasal irrigation was associated with some clinically minor side effects. Interestingly, subjects were able to decrease side effects by adjusting irrigation schedule or salinity. Side effects were not sufficiently bothersome to stop therapy. Compliance with daily therapy was very high and is previously unreported. Although this was consistent with a positive effect on relatively severe symptoms, we believe high compliance also was related to teaching, demonstrated proficiency with nasal irrigation, and close telephone follow-up. One prior study reported subjects’ observation of the first nasal irrigation¹⁵; several studies reported providing some education.^1214,18

Our study has several limitations. It was not blinded or placebo controlled. Blinding subjects to a physical therapy is inherently difficult. Investigators who have tried to use normal saline placebos probably affected outcomes.^14-16 One trial using a fresh water (0% saline) placebo was stopped early when several control subjects developed otitis media.³² The investigators also were unblinded, possibly creating observer bias.

Methodologic and recruitment strengths of this study included effective randomization, matched control group, intention-to-treat analysis, low missing data rates, high compliance rate, and low dropout rate. Clinical strengths included significant findings on most parameters assessed. Particularly intriguing was the decreased use of antibiotics in the experimental group. This study offered strong evidence that nasal irrigation is a safe, effective, and inexpensive (nasal pot, $15; daily therapy, <$1/month) therapy for sinus disease that properly trained patients will use. Although questions about the protocol (schedule, concentration, and buffering) and indications require further study in a more diverse patient population, clinicians may confidently recommend nasal irrigation; it offers significant hope for symptomatic relief and QOL improvement for millions of individuals with sinus disease who often have few therapeutic options.

CONCLUSIONS

Daily hypertonic saline nasal irrigation improves sinus-related QOL, decreases symptoms, and decreases medication use in patients with frequent sinusitis. Primary care physicians can feel comfortable recommending this therapy.

Acknowledgments

We thank Thomas Pasic, MD, Michael McDonald, MD, and Diane Heatley, MD, Department of Otolaryngology, University of Wisconsin, Madison.

Sinusitis is a common clinical problem with significant morbidity and often refractory symptoms that accounted for approximately 26.7 million office and emergency visits and resulted in $5.8 billion spent in direct costs in 1996.¹ Sinusitis was the fifth most common diagnosis for which antibiotics were prescribed from 1985 to 1992.² In 1992, 13 million prescriptions were written for sinusitis, up from 5.8 million in 1985.² The number of US chronic sinusitis cases in 1994 was estimated at 35 million, for a prevalence of 134 per 1000 patients.³ The effect of sinusitis on patients’ quality of life (QOL) is significant and can rate as high as back pain, congestive heart disease, and chronic obstructive pulmonary disease on some measures.⁴

Hypertonic nasal irrigation is a therapy that flushes the nasal cavity with saline solution, facilitating a wash of the structures within. Originally part of the Yogic tradition, this technique is anecdotally regarded as safe and effective; it has been suggested as adjunctive therapy for sinusitis and sinus symptoms.^5-7 Potential efficacy is supported by the observation that hypertonic saline improves mucociliary clearance,⁸ thins mucus,^9,10 and may decrease inflammation.⁸ Optimal irrigant salinity and pH are unclear.^10,11 Several small trials examining nasal irrigation have suggested that nasal irrigation is safe, improves nasal symptoms, and is physically tolerable, but inclusion criteria, intervention protocols, and methodological quality vary.^12-18 Improvement of QOL scores^12-14 and several surrogate measures^14-16 have been reported. No study has rigorously evaluated nasal irrigation over a longer period for its effect on QOL, antibiotic and nasal medication use, symptom severity, compliance, and side effects.

We conducted a randomized controlled trial to test the hypotheses that daily hypertonic saline nasal irrigation improves symptoms, decreases antibiotic and nasal medication use, and improves QOL in adult subjects with a history of sinusitis.

Methods

The study protocol was approved by the University of Wisconsin Health Sciences Human Subjects Committee. Subjects were enrolled from May to August 2000 and, after a study period of 6 months, were exited from November 2000 to February 2001. No prior studies existed at inception to guide sample size estimation. Power calculations performed before study initiation indicated that a sample size of 60 subjects would provide 80% power to detect a 10% difference in the Rhinosinusitis Disability Index (RSDI) between study groups. Due to the high patient burden of this study, we assumed a 25% dropout rate.

Randomization

The randomization scheme was prepared by the Investigational Drug Services of the University of Wisconsin Hospital and Clinics. Subjects were stratified by smoking status and then randomized by using an approximate 2:1 block design, with 10 subjects per block. Therefore 68% of subjects were assigned to the experimental group and 32% to the control group. A 2:1 scheme favoring the experimental group was selected due to resource limitations.

Eligibility criteria and subject recruitment

The recruitment and subject participation scheme is shown in Figure W1 (available on the JFP Web site: http://www.jfponline.com). The billing databases for the University of Wisconsin primary care and Ear, Nose, and Throat (ENT) practices were screened for acute and chronic sinusitis (codes 461 and 473, respectively, from the International Classification of Diseases, Ninth Revision). Patients 18 to 65 years old with 2 episodes of acute sinusitis or 1 episode of chronic sinusitis per year for 2 consecutive years (n = 602) were sent a letter explaining the study and inviting participation, along with an opt-out postcard. If no card was returned, potential subjects were phoned. Exclusion criteria included pregnancy and comorbidity significant enough to preclude travel to an informational meeting or performance of the nasal irrigation technique. Patients indicating “moderate to severe” impact of sinus symptoms on their QOL on a Likert scale of 1 to 7 were invited to attend an informational meeting involving enrollment, randomization, and training (n = 128). Of those potential subjects, 44 declined the meeting or were ineligible; 84 agreed to attend the meeting, 77 attended, and 76 enrolled. Of the initial group of 602 potential subjects, 375 were not contacted because the study census reached intended sample size.

One of us (D.R., R.M., or A.Z.) facilitated each informational meeting of 1 to 6 persons. Sealed envelopes containing the patient’s randomized group assignment were distributed to subjects in the order they entered the room. The group assignment was unknown to the investigator. Subjects broke the seal and learned their assignment. Thereafter, investigators were not blind to subjects’ group assignment. Persons managing and analyzing data also saw unblinded data but had no contact with subjects. Participants heard a brief presentation about sinus disease and its treatment. Nasal irrigation theory and technique were explained. Seventy-six subjects consented and were allocated by their randomized group assignments to experimental (n = 52) or control (n = 24) groups. Control subjects continued treatment of sinus disease in their usual manner. Experimental subjects saw a brief demonstration film, witnessed nasal irrigation by the facilitator, and demonstrated proficiency with the nasal irrigation technique before departure. Subjects were provided all ingredients and materials for 6 months of daily nasal irrigation. Experimental subjects also continued usual care for sinus disease.

Intervention

Subjects in the experimental group were asked to irrigate the nose (150 mL through each nostril) daily for 6 months with the SinuCleanse¹⁹ nasal cup containing 2.0% saline buffered with baking soda (1 heaping teaspoon of canning salt, one half teaspoon of baking soda, and 1 pint of tap water; (Table 1). Solution was mixed fresh every 1 to 2 days. All subjects were phoned at 2 weeks to assess initial compliance with study protocols and thereafter if assessment instruments were not returned promptly.

TABLE 1
Baseline patient characteristics*

Outcome measures

The primary outcomes were QOL scores from 2 validated questionnaires: the general health assessment Medical Outcomes Survey Short Form (SF-12)²⁰ and the RSDI,²¹ a disease-specific instrument assessing QOL in emotional, functional, and physical domains. We reworded the phrase my problem to my sinus symptoms on several RSDI items. Consensus within the research group and among consulted experts was that this minor change facilitated more accurate reading and reporting. We also measured overall sinus symptom severity with a Single-Item Symptom Severity Assessment (SIA): “Please evaluate the overall severity of your sinus symptoms since you enrolled in the study”; higher scores on the Likert scale SIA indicated increased severity. Scales for RSDI and SF-12 ranged from 0 to 100 points, with higher scores indicating better overall QOL. Each was completed at baseline and at 1.5, 3, and 6 months; at the 6-month assessment, subjects were shown their baseline answers for comparison because they had told us they needed to recall answers to past questions. They believed they knew whether they felt better or worse and wanted their later answers to reflect this change. Allowing subjects to view previous scores is an accepted research practice.²² However, because we did not allow subjects to see their baseline answers at 1.5 and 3 months, scores must be interpreted in light of the availability of the baseline data to the subjects.

Secondary outcomes were assessed with multiple methods. Compliance with nasal irrigation was recorded in a daily diary. The presence or absence of sinus symptoms (headache, congestion, facial pressure, facial pain, nasal discharge), antibiotic use, and nasal-spray use was assessed every 2 weeks. An exit questionnaire asked subjects to report categorically whether their sinus-related QOL had gotten worse, stayed the same, or improved, and to estimate the percentage of change (scale from 0 to ±100%). Overall satisfaction and side effects were reported at 6 months.

Statistical methods

Baseline characteristics of experimental and control groups were compared to assess randomization. Analysis, performed on an intention-to-treat basis, involved all 76 subjects randomized into the study. As dictated by the intention-to-treat model, the few missing values were imputed with multiple regression. Repeated measures analysis of variance contrasted the primary outcomes, that is, QOL status and sinus symptom scores within each group at baseline and subsequent periods. Differences between experimental and control groups were analyzed at each point in the repeated measures model and comprehensively for the entire time frame of the study. Statistical significance was assessed with 2-tailed tests. Data are presented as mean values with range of standard error, unless otherwise indicated.

Results

The study sample (Table 1) consisted of 76 subjects (55 female) randomized to experimental (n = 52) and control (n = 24) groups. Subjects’ ages ranged from 19 to 62 years, with a mean age of 42 years. Sixty-nine subjects (46 experimental and 23 control) completed the study. Seven subjects dropped out of the study at 1.5 months or earlier. A phone questionnaire was completed by 3 experimental dropouts; 2 of the 3 identified “lack of time” as the main reason for leaving the study; the remaining subject did not specify a reason. All 3 identified nasal irrigation as “helpful,” and none identified side effects as significant. The remaining 4 subjects were lost to follow-up. Dropouts tended to have slightly better baseline RSDI scores than nondropouts, 66.8 vs 58.1 points, but this difference was not significant (P = .15). No significant baseline differences were found between the groups of mostly white, female, well-educated subjects (Table 1). Baseline RSDI, SF-12, and SIA scores were similar in both groups. Although ENT subjects tended to have slightly worse baseline RSDI and SIA scores and improved slightly more during the study than other experimental subjects, the effect of clinic type (ENT vs primary care) was not statistically significant. By chance all subjects from ENT clinics (n = 6) and a disproportionate percentage of subjects with chronic sinusitis were randomized to the experimental group. Neither variable was statistically significant.

Experimental subjects showed a significant improvement in RSDI scores: 58.4 ± 2.0, 66.6 ± 2.2, 72.4 ± 2.2, and 72.8 ± 2.2 points at baseline, 1.5, 3, and 6 months, respectively (Table 2, Figure 2). Although the difference was not significant (P = .08), experimental subjects whose initial RSDI score was less than 50 points improved the most, with an average score change of 17.8 ± 4.4, and comparable control subjects had an average RSDI score change of 8.8 ± 2.9 points. Emotional and functional RSDI domains were not significantly related to score change; however, the physical domain of the survey was significant (P = .05).

SIA scores for experimental subjects improved (P < .05) at all follow-up points compared with control subjects; scores for the experimental group were 3.9 ± 0.1, 3.1 ± 0.2, 2.7 ± 0.2, and 2.4 ± 0.1 points at baseline, 1.5, 3, and 6 months, respectively (Table 2, Figure 2).

SF-12 score showed no significant differences between groups at any follow-up point but by 6 months trended toward significance (P = .06; Table 2).

Forty-one (93%) experimental subjects completing the exit questionnaire reported improvement. Most (n = 16, 73%) control subjects reported no change, but 18% reported worsening (P < .001; Table 3). Experimental subjects reported an average of 57 ± 4.5% improvement (range, 0–100%), whereas control subjects reported an average of 7 ± 5.9% worsening (range, -80% to 50%; P < .001).

Experimental subjects reported using nasal irrigation on 87% of days during the study; 31 subjects reported using nasal irrigation on 91% or more days, 13 subjects on 76% to 90% of days, and 5 subjects on 51% to 75% of days. Only 3 subjects used nasal irrigation on 50% or fewer days; these 3 subjects had relatively good baseline RSDI and SIA scores compared with other experimental subjects. Compliance was not significantly associated with changes in SIA or RSDI scores. The average survey completion rate was 96% at each assessment by each group.

Experimental subjects spent fewer 2-week blocks with nasal congestion, sinus headache, and frontal pain and pressure and used antibiotics and nasal sprays in fewer blocks (Table 3).

Forty-four experimental subjects answered questions about satisfaction and side effects. Forty-two stated they “will continue to use” nasal irrigation; the remaining 2 subjects found nasal irrigation less helpful but did not experience side effects. All 44 subjects “would recommend” nasal irrigation to friends or family with sinus problems. Ten subjects (23%) experienced side effects; 8 identified nasal irritation, nasal burning, tearing, nosebleeds, headache, or nasal drainage as occurring but “not significant.” Two subjects identified nasal burning, irritation, and headache as “significant,” but this did not change their high satisfaction rating. Of the 10 subjects who experienced side effects, 4 reduced or eliminated the side effects by temporarily alternating treatment days or decreasing salinity by 50%.

TABLE 2
Primary outcomes: RSDI, SF-12, and SIA baseline scores and mean score changes*

TABLE 3
Secondary outcomes

FIGURE 1
Position of nasal cup for nasal irrigation therapy A B

FIGURE 2
Mean RSDI and SIA scores in control and experimental subjects

DISCUSSION

Our trial of daily hypertonic nasal irrigation produced several significant findings. We found consistent, statistically significant improvements in QOL (RSDI) and overall symptom severity (SIA). This was consistent with QOL improvement previously reported over short periods with the use of disease-specific measures.^12-14 The RSDI is a moderately well-developed and validated disease-specific QOL instrument.^21-23 The “minimal clinically important difference,” defined as the average score improvement needed to justify costs and risks,^24-26 has not been established for sinusitis. However, it has been estimated for other disease states. For example, a half-point change on a 7-point Likert scale corresponds to estimates of important change in patients with chronic heart and lung disease.^22,27 Others have found similar relationships.^28-31 In our study, RSDI scores among treated subjects averaged 6.0 and 15.5 points better than controls at 3 and 6 months, respectively. On the SIA, treated subjects averaged 0.6, 0.9, and 1.6 points better. Extrapolating from these findings, these differences appear to be clinically significant. By using 10% improvement of the RSDI, our data showed numbers needed to treat of 9, 5, and 2 at 1.5, 3, and 6 months, respectively (95% confidence interval at 6 months, 1.4–2.6). Numbers needed to treat for SIA, symptom frequency, and medication use were similar. SF-12 improvement, although not statistically significant in this small trial, may represent clinically significant improvements in general health-related QOL.

“Percentage change” is used often by clinicians to gauge therapeutic progress. Ours is the first study to document such change in sinusitis patients using nasal irrigation. Ours is also the first trial to show decreased symptom frequency over a 6-month period. Shorter trials have documented improvement in patients with nasal symptoms^12,13,17,18 or with chronic sinusitis in adult^14,15 and pediatric¹⁶ populations. Consistent with improved symptoms and QOL, experimental subjects decreased their use of antibiotics and nasal sprays, as previously reported in a short trial.¹²

Side effects have not been carefully assessed in previous trials. Although generally safe, daily hypertonic nasal irrigation was associated with some clinically minor side effects. Interestingly, subjects were able to decrease side effects by adjusting irrigation schedule or salinity. Side effects were not sufficiently bothersome to stop therapy. Compliance with daily therapy was very high and is previously unreported. Although this was consistent with a positive effect on relatively severe symptoms, we believe high compliance also was related to teaching, demonstrated proficiency with nasal irrigation, and close telephone follow-up. One prior study reported subjects’ observation of the first nasal irrigation¹⁵; several studies reported providing some education.^1214,18

Our study has several limitations. It was not blinded or placebo controlled. Blinding subjects to a physical therapy is inherently difficult. Investigators who have tried to use normal saline placebos probably affected outcomes.^14-16 One trial using a fresh water (0% saline) placebo was stopped early when several control subjects developed otitis media.³² The investigators also were unblinded, possibly creating observer bias.

Methodologic and recruitment strengths of this study included effective randomization, matched control group, intention-to-treat analysis, low missing data rates, high compliance rate, and low dropout rate. Clinical strengths included significant findings on most parameters assessed. Particularly intriguing was the decreased use of antibiotics in the experimental group. This study offered strong evidence that nasal irrigation is a safe, effective, and inexpensive (nasal pot, $15; daily therapy, <$1/month) therapy for sinus disease that properly trained patients will use. Although questions about the protocol (schedule, concentration, and buffering) and indications require further study in a more diverse patient population, clinicians may confidently recommend nasal irrigation; it offers significant hope for symptomatic relief and QOL improvement for millions of individuals with sinus disease who often have few therapeutic options.

CONCLUSIONS

Daily hypertonic saline nasal irrigation improves sinus-related QOL, decreases symptoms, and decreases medication use in patients with frequent sinusitis. Primary care physicians can feel comfortable recommending this therapy.

Acknowledgments

We thank Thomas Pasic, MD, Michael McDonald, MD, and Diane Heatley, MD, Department of Otolaryngology, University of Wisconsin, Madison.

Clinical trials and meta-analyses of these trials^1-3 have found that antibiotics do not provide clinically relevant improvements in patient outcomes in the treatment of otherwise healthy adults with acute bronchitis. Despite these findings, antibiotics remain the traditional choice of therapy.^4-6 To better understand the process of making a diagnosis and deciding to treat, further study is needed to explore the complex interaction between patients and physicians.

Explanatory models of illness, pioneered by Arthur Kleinman, provide insight into the dynamics of physician and patient processes in a clinical encounter.^7-10 Physician and patient models are elicited through the use of semi-structured, in-depth interviews. The physician’s model has 5 basic topics: etiology, onset of symptoms, pathophysiology, course of illness, and treatment of illness. A patient will generally consider these same issues in a different framework: What caused my illness?, What symptoms have I had?, What does my sickness do to me?, How severe is my sickness?, and What kind of treatment should I receive? The patient model, which is often drawn from cultural traditions and norms and may not be fully articulated, tends to be less abstract, possibly inconsistent, and even self-contradictory. ⁸ Differences between patient and physician explanatory models may lead to conflict, poor communication, low compliance, decreased patient satisfaction, and worse patient outcomes.

The purpose of this study was to elicit and analyze explanatory models to better understand how physicians make the diagnosis of acute bronchitis and decide on treatment for a given patient and describe patient expectations and needs when experiencing an episode of acute bronchitis.

Methods

Participants

This qualitative study used a purposeful, homogeneous sample of 30 family physicians and 30 patients from several types of medical practices in the Dallas, Texas area. It was purposeful in that we deliberately tried to include patients and physicians from a variety of settings. The study was approved by the institutional review boards of University of Texas Southwestern Medical Center and Southern Methodist University.

A letter inviting participation was mailed to physicians. This letter also requested access to adult patients who were seen with an episode of acute bronchitis from 4 weeks to 6 months previously. This mailing was followed by a telephone call from a research assistant to set up an interview. A similar process was followed for patients.

In-depth interviews and data collection

Interview scripts had open-ended questions and standard probes to elicit information about the explanatory model. After obtaining informed consent, interviews were conducted by 1 trained interviewer and audio recorded, transcribed, and checked for accuracy.

Data analysis

An editing style of analysis was used in which the text of the interviews was read line by line and data were grouped into themes.¹¹ Two data management software programs were used to develop codes and labeling, Ethnograph version 4.0 (Qualis Research Association, Salt Lake City, UT) and NVivo (Revision 1.2, Qualitative Solutions and Research Pty Ltd, Cambridge, MA). We explored the data for linkages and connections of the coded groups for hierarchical and non-hierarchical relationships.

The data were analyzed and interpreted by a multidisciplinary team consisting of a family physician (K.C.O.), an epidemiologist (L.M.S.), 2 medical anthropologists (R.P.W., C.S.), a medical anthropology graduate student (K.M.C.), and a qualitative research assistant (O.C.). Through a series of meetings, we shared findings, discussed relationships, explored areas of discrepancy and outlying data, and developed the explanatory models.

Results

Participant demographics are provided in the Table. To contrast models, results are presented for the 5 statements with the patient model followed by the physician model.

TABLE 1
Physician and patient demographic data

What caused my illness/etiology

About one third of the patients felt that their bronchitis was triggered by external factors such as allergies, pollution, smoking, or cold weather. As 1 patient stated, “I think that living here, in being exposed to a lot of pollutants over a period of years, has weakened our bronchial areas and therefore, I am more susceptible to the weather changes, the dampness, wind blowing, cold.”

Approximately one third referred to an infectious agent or an infection causing the bronchitis, using words such as bug and germ. Only 2 patients mentioned the words viral or bacterial and the references were nonspecific. One stated, “I assumed a bug of some sort and I am utterly unclear about, you know, what’s a virus, a bacteria, viral versus bacterial infection.” Others talked about how being stressed or tired lowered their resistance and caused the bronchitis. There was another group of patients who felt that they did not know what caused their bronchitis.

Most physicians reported that acute bronchitis is generally viral, but added that it could also be due to Mycoplasma pneumoniae, Chlamydia pneumoniae, Haemophilus influenzae, or Streptococcal pneumoniae and that it was difficult to say what caused an individual’s illness. Environmental exposures, such as smoking, air pollution, and allergies, were also felt to play a role in etiology. This was typified by 1 physician who stated, “I see it most frequently in people who are smokers or passive smokers.” A few physicians expressed the view that the cause of bronchitis was not really understood.

Symptoms I have had/onset of symptoms

Patients tended to report symptoms in order of occurrence. An example was, “My head stopped up and I felt … head congestion, my chest was congested. Sometimes it was hard for me to breathe, and coughing and sneezing and I hurt.”

Patients were asked to rank their symptoms in order of seriousness. Approximately one third reported coughing as their most serious complaint. Another third listed difficulty breathing. Comments about this symptom reflected a strong sense of concern or fear such as, “I had a hard time breathing at night. That was one of the things that was kind of scary … it was something I couldn’t relate to at first and is probably the worst symptom.” When asked if there was 1 symptom that particularly worried them, coughing was the most common response followed by breathing difficulties and then a wide array of symptoms such as fever and chest pain.

When patients described their cough, there tended to be those who used adjectives such as dry, mild, and tickle, and those who used terms such as deep, substernal, barking, goes down below your hips. The cough was commonly described as productive or nonproductive and ongoing or constant. In general, patients fell into 2 camps: those who reported being sick for a short time (1–3 days) and those who waited longer (1–3 weeks) before going to a doctor. Most patients had experienced prior episodes of bronchitis. Those with more experience tended to feel that they needed to see a physician.

All physicians reported cough as the classic symptom of bronchitis. Approximately half indicated that the cough was typically productive and described the color of the phlegm. The others stated that cough was the classic symptom but did not specify the characteristics. Other symptoms listed were fever, shortness of breath, wheezing, congestion, malaise, aches, and chills.

When patients were asked what they felt would be the most worrisome symptom of bronchitis, over two thirds reported coughing, especially when it affected sleep or work functioning and was persistent and productive. When reporting their own most worrisome symptoms, however, physicians listed high fever, chest pain, or purulent sputum and were concerned about serious underlying diseases such as pneumonia.

Physicians felt there was wide variation in the time that patients with bronchitis symptoms waited to be seen. Approximately half of the physicians reported that patients were sick for 1 week or less before their appointment. The other half reported wide intervals ranging from 1 day to 3 weeks.

What my sickness did to me/pathophysiology

Most patients responded that they had never thought about what the illness did to them. When probed, patients generally responded that they had an infection “in the bronchial pipes” or a “cold in the chest.”

Physicians were asked to describe the pathophysiology of acute bronchitis and discuss how they arrive at a diagnosis. In general, they described how a virus or bacteria “invades” the respiratory tract, causing inflammation of the airways and bronchioles, resulting in increased mucus production. Several physicians described bacterial overgrowth occurring. Physicians separated acute bronchitis from an upper respiratory infection based on the cough, especially if it was productive, and from pneumonia by the absence of more severe signs or symptoms, such as high fever, shortness of breath, or presence of rales. Several physicians tied their diagnosis to treatment, as illustrated by a physician who stated, “I think that many doctors use bronchitis as the excuse to give an antibiotic. And I sometimes fall into that trap. So if I want them to think they deserve an antibiotic, then sometimes I will give them the diagnosis of bronchitis.”

How severe is my sickness/course of illness

One third of patients reported feeling very bad and one third felt moderately bad. The remainder reported variability in the way they felt or not feeling ill at all. Similarly, one third reported a cough duration of 3 weeks or longer and one third felt that the illness had a major impact on their work and daily routine. When asked what would have happened if they had not seen the doctor, patients consistently reported that they would have been sick longer, would not have recovered, or would have gotten pneumonia. Three patients felt they could have died. None said that they would have recovered on their own.

Physicians were asked how many days of work were missed by patients with acute bronchitis. More than two thirds estimated that patients missed from 1 to 3 days. A number of physicians mentioned that factors such as work motivation, attitudes about illness, and availability of paid sick leave influenced the number of days off. Most physicians thought it would take patients 1 week or longer before they felt well enough to return to their normal routine.

What kind of treatment should I receive/treatment

All patients recalled that the primary treatment for their acute bronchitis was a prescription medication such as an antibiotic, cough suppressant, or decongestant. Twenty-seven reported receiving an antibiotic prescription. An inhaler was prescribed for about one third of patients. Several patients commented on the inhaler’s effectiveness for relieving symptoms. This is illustrated by a patient who stated, “the inhaler is the thing that helped me instantaneously.” About one third of patients reported receiving medical advice such as drinking lots of liquids and resting.

Most patients agreed that the treatment they received was what they expected, but when asked to articulate what they “expected,” they had problems doing so. After probing by the interviewer, more than 50% stated that an antibiotic was what they needed for treating their illness. This is typified by the response of one patient, “I would like [bronchitis] to be treated more aggressively. … [Physicians] want to wait until you’ve got a full blown infection before they do anything and I wish that would be different next time.”

When patients were asked about treatment satisfaction, about two thirds reported that they were satisfied because they felt better “pretty fast.” There was wide variation in their definition of “pretty fast,” ranging from 1 day to 3 weeks. Several patients were somewhat dissatisfied with their treatment but felt that nothing else could have been done. A few patients expressed strong dissatisfaction because of slow recovery time or because the prescribed medications did not relieve the symptoms.

Two major treatment approaches emerged from the physician interviews: use of antibiotics or a primary focus on symptom relief. Most physicians who commonly used antibiotics were concerned about which antibiotics were more effective. They also were concerned about patients who were sick longer than 1 week, had discolored sputum, were members of high-risk populations (especially smokers), and who did not improve with treatment. A few physicians who focused on symptom relief prescribed cough suppressants, ß-agonist inhalers, or decongestants. These physicians felt it was important to educate patients about differences between viral and bacterial diseases, disadvantages of overusing antibiotics, and ways to relieve symptoms at home instead of relying on prescribed medications.

When asked about expectations of treatment, all 30 physicians thought that their patients wanted them to prescribe antibiotics. About one third reported that patients also expected to have a “prescribed cough medicine.” Three fourths of the physicians perceived patients’ “antibiotic expectations” as a pressure, although with different rationales. Several physicians admitted that they prescribed antibiotics “to make the patient happy.” One said, “I think people expect it. If you get somebody that has come in and has done everything they can figure out to do to try to get better, then you can certainly end up with patients that are unhappy if you refuse to give them antibiotics.” Some physicians suggested that the pressure of prescribing antibiotics was not from the individual, but from the system, including the employer, the legal system, and the health insurance system.

Physicians who did not feel pressure to prescribe antibiotics could be grouped into those who usually used antibiotics to treat acute bronchitis and those who took time to explain to their patients why they did not want to prescribe antibiotics. Some quotations that illustrate the views of this latter group were: “Usually I try to involve the patient in my thinking, until we feel some sort of consensus” and “I basically lay out why I’m not [prescribing an antibiotic].” A synopsis of the models is presented in Figure 1.

FIGURE 1

Discussion

It is well recognized in the literature that antibiotic usage in the therapy of acute bronchitis in the otherwise healthy adult (1) does not confer a clinically relevant shorter course of illness, (2) does not prevent the rare progression to pneumonia any better than placebo, (3) has a significantly negative impact on public health by contributing to antibiotic resistance, and thus (4) is not warranted.^1-3,5,12,13 Nevertheless, antibiotic usage patterns have not changed significantly in the past 10 years, and antibiotics are still the traditional first-line therapy in practice. Reasons for this dichotomy are complex. The purpose of this qualitative study was to begin to clarify some of the complexities by determining incongruous areas of patient and physician beliefs regarding the diagnosis and management of acute bronchitis. Similarities and differences in 3 areas of patient and physician models warrant further discussion: etiology of acute bronchitis, course if untreated, and factors affecting the decision to treat.

Patients in this study had a vague understanding of the concept of infection and differences between bacteria and viruses. This finding has been reported in other patient-centered studies^13-15 regarding respiratory infections and is likely due to inadequate or contradictory information imparted by the medical community through individual physician-specific communications and from the medical system as a whole. In contrast, physicians in the study uniformly noted a viral cause of most cases of bronchitis but often qualified the statements with concern of not knowing which individuals might have bacterial infections and the lack of tools to distinguish between viral and bacterial etiologies.

Further complicating this paradigm of conflict and confusion regarding viral and bacterial causes, patients consistently thought that not treating acute bronchitis with antibiotics would lead to prolonged, worsening, and potentially life-threatening illness. There is a lack of understanding among patients that acute bronchitis often results in a cough lasting longer than 2 weeks, and this may contribute to the misconception that prolonged duration of illness is evidence of more serious infection.

One cannot separate these 2 themes—confusion regarding etiology and miscommunication about the clinical course of untreated illness—from the decision to treat and the role of antibiotics. From the patients’ perspective, without antibiotics they would not get better. Compounding this belief is the patients’ urgent desire for symptom relief. Physicians reported significant internal conflict regarding treatment, characterized by a recognition that antibiotics were of little value, a universal assumption that patients expected antibiotics, a desire for patient satisfaction, perceived pressures from employers, and a fear of “missing” a more serious disease or making a mistake (from the desire to heal and the fear of medicolegal actions). These complex and conflicting perceptions, emotions, and cognitions are illustrated in Figure 2.

Over the past several decades, medical and lay traditions have evolved to imply that productive coughs with green-yellow sputum or colds with green-yellow nasal discharge represent bacterial infections or something that requires an antibiotic.^4,5,16,17 Randomized clinical trials have not shown that treatment with antibiotics leads to significantly improved clinical outcomes.^1-3,5 In a study of 1398 children, Vinson and Lutz reported that parental expectation of an antibiotic was second only to the presence of rales in increasing the likelihood of the diagnosis of bronchitis.¹⁸ With little in history or examination to distinguish between viral and bacterial infections and the fear of “missing something,” the presence or absence of yellow-green nasal secretions and sputum have become the “key” questions in our medical history. This has created a medical tradition that falsely implies to patients a different illness or outcome from those without secretion production or clear discharge. Is it any surprise that patients expect antibiotics?

In evaluating the generalizability of this study, potential biases and limitations of qualitative studies should be considered. First, the creation of this explanatory model was designed to generate ideas and hypotheses, not to test them. Second, the views represented were from a single medical specialty in one geographic area and based on physicians’ and patients’ subjective perceptions. Nevertheless, the goal of such a study was to provide a theoretical model of communication between patient and physician that generates questions for further exploration and areas for potential intervention.

In summary, if, as a medical community, we hope to develop new strategies to decrease unwarranted antibiotic usage, we need to educate patients and health care professionals regarding the causation and natural history of respiratory infections. Gonzales and associates reported impressive results with office-based interventions targeting physicians and patients, and this work needs to be generalized.^19,20 However, until there is a major public health emphasis on education at the community level regarding respiratory infections concurrent with an educational effort targeted for health care professionals to dispel the “myth” that characteristics of sputum and nasal discharge are good predictors of clinical outcomes, progress will be slow. To enhance communication between patient and physician, it is important that we elicit and appropriately address patient fears and concerns regarding the natural course of illness with an episode of bronchitis.

FIGURE 2

Clinical trials and meta-analyses of these trials^1-3 have found that antibiotics do not provide clinically relevant improvements in patient outcomes in the treatment of otherwise healthy adults with acute bronchitis. Despite these findings, antibiotics remain the traditional choice of therapy.^4-6 To better understand the process of making a diagnosis and deciding to treat, further study is needed to explore the complex interaction between patients and physicians.

Explanatory models of illness, pioneered by Arthur Kleinman, provide insight into the dynamics of physician and patient processes in a clinical encounter.^7-10 Physician and patient models are elicited through the use of semi-structured, in-depth interviews. The physician’s model has 5 basic topics: etiology, onset of symptoms, pathophysiology, course of illness, and treatment of illness. A patient will generally consider these same issues in a different framework: What caused my illness?, What symptoms have I had?, What does my sickness do to me?, How severe is my sickness?, and What kind of treatment should I receive? The patient model, which is often drawn from cultural traditions and norms and may not be fully articulated, tends to be less abstract, possibly inconsistent, and even self-contradictory. ⁸ Differences between patient and physician explanatory models may lead to conflict, poor communication, low compliance, decreased patient satisfaction, and worse patient outcomes.

The purpose of this study was to elicit and analyze explanatory models to better understand how physicians make the diagnosis of acute bronchitis and decide on treatment for a given patient and describe patient expectations and needs when experiencing an episode of acute bronchitis.

Methods

Participants

This qualitative study used a purposeful, homogeneous sample of 30 family physicians and 30 patients from several types of medical practices in the Dallas, Texas area. It was purposeful in that we deliberately tried to include patients and physicians from a variety of settings. The study was approved by the institutional review boards of University of Texas Southwestern Medical Center and Southern Methodist University.

A letter inviting participation was mailed to physicians. This letter also requested access to adult patients who were seen with an episode of acute bronchitis from 4 weeks to 6 months previously. This mailing was followed by a telephone call from a research assistant to set up an interview. A similar process was followed for patients.

In-depth interviews and data collection

Interview scripts had open-ended questions and standard probes to elicit information about the explanatory model. After obtaining informed consent, interviews were conducted by 1 trained interviewer and audio recorded, transcribed, and checked for accuracy.

Data analysis

An editing style of analysis was used in which the text of the interviews was read line by line and data were grouped into themes.¹¹ Two data management software programs were used to develop codes and labeling, Ethnograph version 4.0 (Qualis Research Association, Salt Lake City, UT) and NVivo (Revision 1.2, Qualitative Solutions and Research Pty Ltd, Cambridge, MA). We explored the data for linkages and connections of the coded groups for hierarchical and non-hierarchical relationships.

The data were analyzed and interpreted by a multidisciplinary team consisting of a family physician (K.C.O.), an epidemiologist (L.M.S.), 2 medical anthropologists (R.P.W., C.S.), a medical anthropology graduate student (K.M.C.), and a qualitative research assistant (O.C.). Through a series of meetings, we shared findings, discussed relationships, explored areas of discrepancy and outlying data, and developed the explanatory models.

Results

Participant demographics are provided in the Table. To contrast models, results are presented for the 5 statements with the patient model followed by the physician model.

TABLE 1
Physician and patient demographic data

What caused my illness/etiology

About one third of the patients felt that their bronchitis was triggered by external factors such as allergies, pollution, smoking, or cold weather. As 1 patient stated, “I think that living here, in being exposed to a lot of pollutants over a period of years, has weakened our bronchial areas and therefore, I am more susceptible to the weather changes, the dampness, wind blowing, cold.”

Approximately one third referred to an infectious agent or an infection causing the bronchitis, using words such as bug and germ. Only 2 patients mentioned the words viral or bacterial and the references were nonspecific. One stated, “I assumed a bug of some sort and I am utterly unclear about, you know, what’s a virus, a bacteria, viral versus bacterial infection.” Others talked about how being stressed or tired lowered their resistance and caused the bronchitis. There was another group of patients who felt that they did not know what caused their bronchitis.

Most physicians reported that acute bronchitis is generally viral, but added that it could also be due to Mycoplasma pneumoniae, Chlamydia pneumoniae, Haemophilus influenzae, or Streptococcal pneumoniae and that it was difficult to say what caused an individual’s illness. Environmental exposures, such as smoking, air pollution, and allergies, were also felt to play a role in etiology. This was typified by 1 physician who stated, “I see it most frequently in people who are smokers or passive smokers.” A few physicians expressed the view that the cause of bronchitis was not really understood.

Symptoms I have had/onset of symptoms

Patients tended to report symptoms in order of occurrence. An example was, “My head stopped up and I felt … head congestion, my chest was congested. Sometimes it was hard for me to breathe, and coughing and sneezing and I hurt.”

Patients were asked to rank their symptoms in order of seriousness. Approximately one third reported coughing as their most serious complaint. Another third listed difficulty breathing. Comments about this symptom reflected a strong sense of concern or fear such as, “I had a hard time breathing at night. That was one of the things that was kind of scary … it was something I couldn’t relate to at first and is probably the worst symptom.” When asked if there was 1 symptom that particularly worried them, coughing was the most common response followed by breathing difficulties and then a wide array of symptoms such as fever and chest pain.

When patients described their cough, there tended to be those who used adjectives such as dry, mild, and tickle, and those who used terms such as deep, substernal, barking, goes down below your hips. The cough was commonly described as productive or nonproductive and ongoing or constant. In general, patients fell into 2 camps: those who reported being sick for a short time (1–3 days) and those who waited longer (1–3 weeks) before going to a doctor. Most patients had experienced prior episodes of bronchitis. Those with more experience tended to feel that they needed to see a physician.

All physicians reported cough as the classic symptom of bronchitis. Approximately half indicated that the cough was typically productive and described the color of the phlegm. The others stated that cough was the classic symptom but did not specify the characteristics. Other symptoms listed were fever, shortness of breath, wheezing, congestion, malaise, aches, and chills.

When patients were asked what they felt would be the most worrisome symptom of bronchitis, over two thirds reported coughing, especially when it affected sleep or work functioning and was persistent and productive. When reporting their own most worrisome symptoms, however, physicians listed high fever, chest pain, or purulent sputum and were concerned about serious underlying diseases such as pneumonia.

Physicians felt there was wide variation in the time that patients with bronchitis symptoms waited to be seen. Approximately half of the physicians reported that patients were sick for 1 week or less before their appointment. The other half reported wide intervals ranging from 1 day to 3 weeks.

What my sickness did to me/pathophysiology

Most patients responded that they had never thought about what the illness did to them. When probed, patients generally responded that they had an infection “in the bronchial pipes” or a “cold in the chest.”

Physicians were asked to describe the pathophysiology of acute bronchitis and discuss how they arrive at a diagnosis. In general, they described how a virus or bacteria “invades” the respiratory tract, causing inflammation of the airways and bronchioles, resulting in increased mucus production. Several physicians described bacterial overgrowth occurring. Physicians separated acute bronchitis from an upper respiratory infection based on the cough, especially if it was productive, and from pneumonia by the absence of more severe signs or symptoms, such as high fever, shortness of breath, or presence of rales. Several physicians tied their diagnosis to treatment, as illustrated by a physician who stated, “I think that many doctors use bronchitis as the excuse to give an antibiotic. And I sometimes fall into that trap. So if I want them to think they deserve an antibiotic, then sometimes I will give them the diagnosis of bronchitis.”

How severe is my sickness/course of illness

One third of patients reported feeling very bad and one third felt moderately bad. The remainder reported variability in the way they felt or not feeling ill at all. Similarly, one third reported a cough duration of 3 weeks or longer and one third felt that the illness had a major impact on their work and daily routine. When asked what would have happened if they had not seen the doctor, patients consistently reported that they would have been sick longer, would not have recovered, or would have gotten pneumonia. Three patients felt they could have died. None said that they would have recovered on their own.

Physicians were asked how many days of work were missed by patients with acute bronchitis. More than two thirds estimated that patients missed from 1 to 3 days. A number of physicians mentioned that factors such as work motivation, attitudes about illness, and availability of paid sick leave influenced the number of days off. Most physicians thought it would take patients 1 week or longer before they felt well enough to return to their normal routine.

What kind of treatment should I receive/treatment

All patients recalled that the primary treatment for their acute bronchitis was a prescription medication such as an antibiotic, cough suppressant, or decongestant. Twenty-seven reported receiving an antibiotic prescription. An inhaler was prescribed for about one third of patients. Several patients commented on the inhaler’s effectiveness for relieving symptoms. This is illustrated by a patient who stated, “the inhaler is the thing that helped me instantaneously.” About one third of patients reported receiving medical advice such as drinking lots of liquids and resting.

Most patients agreed that the treatment they received was what they expected, but when asked to articulate what they “expected,” they had problems doing so. After probing by the interviewer, more than 50% stated that an antibiotic was what they needed for treating their illness. This is typified by the response of one patient, “I would like [bronchitis] to be treated more aggressively. … [Physicians] want to wait until you’ve got a full blown infection before they do anything and I wish that would be different next time.”

When patients were asked about treatment satisfaction, about two thirds reported that they were satisfied because they felt better “pretty fast.” There was wide variation in their definition of “pretty fast,” ranging from 1 day to 3 weeks. Several patients were somewhat dissatisfied with their treatment but felt that nothing else could have been done. A few patients expressed strong dissatisfaction because of slow recovery time or because the prescribed medications did not relieve the symptoms.

Two major treatment approaches emerged from the physician interviews: use of antibiotics or a primary focus on symptom relief. Most physicians who commonly used antibiotics were concerned about which antibiotics were more effective. They also were concerned about patients who were sick longer than 1 week, had discolored sputum, were members of high-risk populations (especially smokers), and who did not improve with treatment. A few physicians who focused on symptom relief prescribed cough suppressants, ß-agonist inhalers, or decongestants. These physicians felt it was important to educate patients about differences between viral and bacterial diseases, disadvantages of overusing antibiotics, and ways to relieve symptoms at home instead of relying on prescribed medications.

When asked about expectations of treatment, all 30 physicians thought that their patients wanted them to prescribe antibiotics. About one third reported that patients also expected to have a “prescribed cough medicine.” Three fourths of the physicians perceived patients’ “antibiotic expectations” as a pressure, although with different rationales. Several physicians admitted that they prescribed antibiotics “to make the patient happy.” One said, “I think people expect it. If you get somebody that has come in and has done everything they can figure out to do to try to get better, then you can certainly end up with patients that are unhappy if you refuse to give them antibiotics.” Some physicians suggested that the pressure of prescribing antibiotics was not from the individual, but from the system, including the employer, the legal system, and the health insurance system.

Physicians who did not feel pressure to prescribe antibiotics could be grouped into those who usually used antibiotics to treat acute bronchitis and those who took time to explain to their patients why they did not want to prescribe antibiotics. Some quotations that illustrate the views of this latter group were: “Usually I try to involve the patient in my thinking, until we feel some sort of consensus” and “I basically lay out why I’m not [prescribing an antibiotic].” A synopsis of the models is presented in Figure 1.

FIGURE 1

Discussion

It is well recognized in the literature that antibiotic usage in the therapy of acute bronchitis in the otherwise healthy adult (1) does not confer a clinically relevant shorter course of illness, (2) does not prevent the rare progression to pneumonia any better than placebo, (3) has a significantly negative impact on public health by contributing to antibiotic resistance, and thus (4) is not warranted.^1-3,5,12,13 Nevertheless, antibiotic usage patterns have not changed significantly in the past 10 years, and antibiotics are still the traditional first-line therapy in practice. Reasons for this dichotomy are complex. The purpose of this qualitative study was to begin to clarify some of the complexities by determining incongruous areas of patient and physician beliefs regarding the diagnosis and management of acute bronchitis. Similarities and differences in 3 areas of patient and physician models warrant further discussion: etiology of acute bronchitis, course if untreated, and factors affecting the decision to treat.

Patients in this study had a vague understanding of the concept of infection and differences between bacteria and viruses. This finding has been reported in other patient-centered studies^13-15 regarding respiratory infections and is likely due to inadequate or contradictory information imparted by the medical community through individual physician-specific communications and from the medical system as a whole. In contrast, physicians in the study uniformly noted a viral cause of most cases of bronchitis but often qualified the statements with concern of not knowing which individuals might have bacterial infections and the lack of tools to distinguish between viral and bacterial etiologies.

Further complicating this paradigm of conflict and confusion regarding viral and bacterial causes, patients consistently thought that not treating acute bronchitis with antibiotics would lead to prolonged, worsening, and potentially life-threatening illness. There is a lack of understanding among patients that acute bronchitis often results in a cough lasting longer than 2 weeks, and this may contribute to the misconception that prolonged duration of illness is evidence of more serious infection.

One cannot separate these 2 themes—confusion regarding etiology and miscommunication about the clinical course of untreated illness—from the decision to treat and the role of antibiotics. From the patients’ perspective, without antibiotics they would not get better. Compounding this belief is the patients’ urgent desire for symptom relief. Physicians reported significant internal conflict regarding treatment, characterized by a recognition that antibiotics were of little value, a universal assumption that patients expected antibiotics, a desire for patient satisfaction, perceived pressures from employers, and a fear of “missing” a more serious disease or making a mistake (from the desire to heal and the fear of medicolegal actions). These complex and conflicting perceptions, emotions, and cognitions are illustrated in Figure 2.

Over the past several decades, medical and lay traditions have evolved to imply that productive coughs with green-yellow sputum or colds with green-yellow nasal discharge represent bacterial infections or something that requires an antibiotic.^4,5,16,17 Randomized clinical trials have not shown that treatment with antibiotics leads to significantly improved clinical outcomes.^1-3,5 In a study of 1398 children, Vinson and Lutz reported that parental expectation of an antibiotic was second only to the presence of rales in increasing the likelihood of the diagnosis of bronchitis.¹⁸ With little in history or examination to distinguish between viral and bacterial infections and the fear of “missing something,” the presence or absence of yellow-green nasal secretions and sputum have become the “key” questions in our medical history. This has created a medical tradition that falsely implies to patients a different illness or outcome from those without secretion production or clear discharge. Is it any surprise that patients expect antibiotics?

In evaluating the generalizability of this study, potential biases and limitations of qualitative studies should be considered. First, the creation of this explanatory model was designed to generate ideas and hypotheses, not to test them. Second, the views represented were from a single medical specialty in one geographic area and based on physicians’ and patients’ subjective perceptions. Nevertheless, the goal of such a study was to provide a theoretical model of communication between patient and physician that generates questions for further exploration and areas for potential intervention.

In summary, if, as a medical community, we hope to develop new strategies to decrease unwarranted antibiotic usage, we need to educate patients and health care professionals regarding the causation and natural history of respiratory infections. Gonzales and associates reported impressive results with office-based interventions targeting physicians and patients, and this work needs to be generalized.^19,20 However, until there is a major public health emphasis on education at the community level regarding respiratory infections concurrent with an educational effort targeted for health care professionals to dispel the “myth” that characteristics of sputum and nasal discharge are good predictors of clinical outcomes, progress will be slow. To enhance communication between patient and physician, it is important that we elicit and appropriately address patient fears and concerns regarding the natural course of illness with an episode of bronchitis.

FIGURE 2

Clinical trials and meta-analyses of these trials^1-3 have found that antibiotics do not provide clinically relevant improvements in patient outcomes in the treatment of otherwise healthy adults with acute bronchitis. Despite these findings, antibiotics remain the traditional choice of therapy.^4-6 To better understand the process of making a diagnosis and deciding to treat, further study is needed to explore the complex interaction between patients and physicians.

Explanatory models of illness, pioneered by Arthur Kleinman, provide insight into the dynamics of physician and patient processes in a clinical encounter.^7-10 Physician and patient models are elicited through the use of semi-structured, in-depth interviews. The physician’s model has 5 basic topics: etiology, onset of symptoms, pathophysiology, course of illness, and treatment of illness. A patient will generally consider these same issues in a different framework: What caused my illness?, What symptoms have I had?, What does my sickness do to me?, How severe is my sickness?, and What kind of treatment should I receive? The patient model, which is often drawn from cultural traditions and norms and may not be fully articulated, tends to be less abstract, possibly inconsistent, and even self-contradictory. ⁸ Differences between patient and physician explanatory models may lead to conflict, poor communication, low compliance, decreased patient satisfaction, and worse patient outcomes.

The purpose of this study was to elicit and analyze explanatory models to better understand how physicians make the diagnosis of acute bronchitis and decide on treatment for a given patient and describe patient expectations and needs when experiencing an episode of acute bronchitis.

Methods

Participants

This qualitative study used a purposeful, homogeneous sample of 30 family physicians and 30 patients from several types of medical practices in the Dallas, Texas area. It was purposeful in that we deliberately tried to include patients and physicians from a variety of settings. The study was approved by the institutional review boards of University of Texas Southwestern Medical Center and Southern Methodist University.

A letter inviting participation was mailed to physicians. This letter also requested access to adult patients who were seen with an episode of acute bronchitis from 4 weeks to 6 months previously. This mailing was followed by a telephone call from a research assistant to set up an interview. A similar process was followed for patients.

In-depth interviews and data collection

Interview scripts had open-ended questions and standard probes to elicit information about the explanatory model. After obtaining informed consent, interviews were conducted by 1 trained interviewer and audio recorded, transcribed, and checked for accuracy.

Data analysis

An editing style of analysis was used in which the text of the interviews was read line by line and data were grouped into themes.¹¹ Two data management software programs were used to develop codes and labeling, Ethnograph version 4.0 (Qualis Research Association, Salt Lake City, UT) and NVivo (Revision 1.2, Qualitative Solutions and Research Pty Ltd, Cambridge, MA). We explored the data for linkages and connections of the coded groups for hierarchical and non-hierarchical relationships.

The data were analyzed and interpreted by a multidisciplinary team consisting of a family physician (K.C.O.), an epidemiologist (L.M.S.), 2 medical anthropologists (R.P.W., C.S.), a medical anthropology graduate student (K.M.C.), and a qualitative research assistant (O.C.). Through a series of meetings, we shared findings, discussed relationships, explored areas of discrepancy and outlying data, and developed the explanatory models.

Results

Participant demographics are provided in the Table. To contrast models, results are presented for the 5 statements with the patient model followed by the physician model.

TABLE 1
Physician and patient demographic data