Cleveland Clinic Journal of Medicine

A 64-year-old man with end-stage renal disease was evaluated in the pulmonary clinic for persistent abnormalities on axial computed tomography (CT) of the chest. He was a lifelong nonsmoker and had no history of exposure to occupational dust or fumes. His oxygen saturation was 100% on room air, and he denied any respiratory symptoms.

WHEN TO CONSIDER METASTATIC PULMONARY CALCIFICATION

The differential diagnosis for chronic upper-lobe-predominant ground-glass nodules is broad and includes atypical infections, recurrent alveolar hemorrhage, hypersensitivity pneumonitis, vasculitis, sarcoidosis, chronic eosinophilic pneumonia, occupational lung disease, and pulmonary alveolar microlithiasis. However, several aspects of our patient’s case suggested an often overlooked diagnosis, metastatic pulmonary calcification.

Metastatic pulmonary calcification is caused by deposition of calcium salts in lung tissue and is most commonly seen in patients on dialysis,^1,2 and our patient had been dependent on dialysis for many years. The chronically elevated calcium-phosphorus product and secondary hyperparathyroidism often seen with end-stage renal disease may explain this association.

Our patient’s lack of symptoms is also an important diagnostic clue. Unlike many other causes of chronic upper-lobe-predominant ground-glass nodules, metastatic pulmonary calcification does not usually cause symptoms and is often identified only at autopsy.³ Results of pulmonary function testing are often normal.⁴

Metastatic pulmonary calcification can appear as diffusely calcified nodules or high-attenuation areas of consolidation on CT. However, as in our patient’s case, CT may demonstrate fluffy, centrilobular ground-glass nodules due to the microscopic size of the deposited calcium crystals.¹ Identifying calcified vessels on imaging supports the diagnosis.⁴

Treatment of metastatic pulmonary calcification in a patient with end-stage renal disease is focused on correcting underlying metabolic abnormalities with phosphate binders, vitamin D supplementation, and dialysis.

A 64-year-old man with end-stage renal disease was evaluated in the pulmonary clinic for persistent abnormalities on axial computed tomography (CT) of the chest. He was a lifelong nonsmoker and had no history of exposure to occupational dust or fumes. His oxygen saturation was 100% on room air, and he denied any respiratory symptoms.

WHEN TO CONSIDER METASTATIC PULMONARY CALCIFICATION

The differential diagnosis for chronic upper-lobe-predominant ground-glass nodules is broad and includes atypical infections, recurrent alveolar hemorrhage, hypersensitivity pneumonitis, vasculitis, sarcoidosis, chronic eosinophilic pneumonia, occupational lung disease, and pulmonary alveolar microlithiasis. However, several aspects of our patient’s case suggested an often overlooked diagnosis, metastatic pulmonary calcification.

Metastatic pulmonary calcification is caused by deposition of calcium salts in lung tissue and is most commonly seen in patients on dialysis,^1,2 and our patient had been dependent on dialysis for many years. The chronically elevated calcium-phosphorus product and secondary hyperparathyroidism often seen with end-stage renal disease may explain this association.

Our patient’s lack of symptoms is also an important diagnostic clue. Unlike many other causes of chronic upper-lobe-predominant ground-glass nodules, metastatic pulmonary calcification does not usually cause symptoms and is often identified only at autopsy.³ Results of pulmonary function testing are often normal.⁴

Metastatic pulmonary calcification can appear as diffusely calcified nodules or high-attenuation areas of consolidation on CT. However, as in our patient’s case, CT may demonstrate fluffy, centrilobular ground-glass nodules due to the microscopic size of the deposited calcium crystals.¹ Identifying calcified vessels on imaging supports the diagnosis.⁴

Treatment of metastatic pulmonary calcification in a patient with end-stage renal disease is focused on correcting underlying metabolic abnormalities with phosphate binders, vitamin D supplementation, and dialysis.

A 64-year-old man with end-stage renal disease was evaluated in the pulmonary clinic for persistent abnormalities on axial computed tomography (CT) of the chest. He was a lifelong nonsmoker and had no history of exposure to occupational dust or fumes. His oxygen saturation was 100% on room air, and he denied any respiratory symptoms.

WHEN TO CONSIDER METASTATIC PULMONARY CALCIFICATION

The differential diagnosis for chronic upper-lobe-predominant ground-glass nodules is broad and includes atypical infections, recurrent alveolar hemorrhage, hypersensitivity pneumonitis, vasculitis, sarcoidosis, chronic eosinophilic pneumonia, occupational lung disease, and pulmonary alveolar microlithiasis. However, several aspects of our patient’s case suggested an often overlooked diagnosis, metastatic pulmonary calcification.

Metastatic pulmonary calcification is caused by deposition of calcium salts in lung tissue and is most commonly seen in patients on dialysis,^1,2 and our patient had been dependent on dialysis for many years. The chronically elevated calcium-phosphorus product and secondary hyperparathyroidism often seen with end-stage renal disease may explain this association.

Our patient’s lack of symptoms is also an important diagnostic clue. Unlike many other causes of chronic upper-lobe-predominant ground-glass nodules, metastatic pulmonary calcification does not usually cause symptoms and is often identified only at autopsy.³ Results of pulmonary function testing are often normal.⁴

Metastatic pulmonary calcification can appear as diffusely calcified nodules or high-attenuation areas of consolidation on CT. However, as in our patient’s case, CT may demonstrate fluffy, centrilobular ground-glass nodules due to the microscopic size of the deposited calcium crystals.¹ Identifying calcified vessels on imaging supports the diagnosis.⁴

Treatment of metastatic pulmonary calcification in a patient with end-stage renal disease is focused on correcting underlying metabolic abnormalities with phosphate binders, vitamin D supplementation, and dialysis.

To the Editor: We read with great interest the article by Patnaik et al¹ about a patient who had a cardiac metastasis of ovarian cancer, and we would like to raise a few points.

It is important to clarify that metastatic cardiac tumors are not necessary malignant. Intravenous leiomyomatosis is a benign small-muscle tumor that can spread to the heart, causing various cardiac symptoms.² Even with extensive disease, patients with intravenous leiomyomatosis may remain asymptomatic until cardiac involvement occurs. The most common cardiac symptoms are dyspnea, syncope, and lower-extremity edema.

Cardiac involvement in intravenous leiomyomatosis may occur via direct invasion or hematogenous or lymphatic spread of the tumor. In leiomyoma and leiomyosarcoma, cardiac invasion usually occurs via direct spread through the inferior vena cava into the right atrium and ventricle. Thus, cardiac involvement with these tumors (except for nephroma) was reported to exclusively involve the right side of the heart.

In 2014, we reported a unique case of intravenous leiomyomatosis that extended from the right side into the left side of the heart and the aorta via an atrial septal defect.² Intracardiac extension of intravenous leiomyomatosis may result in pulmonary embolism, systemic embolization if involving the left side, and, rarely, sudden death.²

In patients with malignancy, differentiating between thrombosis and tumor is critical. These patients have a hypercoagulable state and a fourfold increase in thrombosis risk, and chemotherapy increases this risk even more.³ Although tissue pathology examination is important for differentiating thrombosis from tumor, visualization of the direct extension of the mass from the primary source into the heart through the inferior vena cava by ultrasonography, computed tomography, or magnetic resonance imaging may help in making this distinction.²

To the Editor: We read with great interest the article by Patnaik et al¹ about a patient who had a cardiac metastasis of ovarian cancer, and we would like to raise a few points.

It is important to clarify that metastatic cardiac tumors are not necessary malignant. Intravenous leiomyomatosis is a benign small-muscle tumor that can spread to the heart, causing various cardiac symptoms.² Even with extensive disease, patients with intravenous leiomyomatosis may remain asymptomatic until cardiac involvement occurs. The most common cardiac symptoms are dyspnea, syncope, and lower-extremity edema.

Cardiac involvement in intravenous leiomyomatosis may occur via direct invasion or hematogenous or lymphatic spread of the tumor. In leiomyoma and leiomyosarcoma, cardiac invasion usually occurs via direct spread through the inferior vena cava into the right atrium and ventricle. Thus, cardiac involvement with these tumors (except for nephroma) was reported to exclusively involve the right side of the heart.

In 2014, we reported a unique case of intravenous leiomyomatosis that extended from the right side into the left side of the heart and the aorta via an atrial septal defect.² Intracardiac extension of intravenous leiomyomatosis may result in pulmonary embolism, systemic embolization if involving the left side, and, rarely, sudden death.²

In patients with malignancy, differentiating between thrombosis and tumor is critical. These patients have a hypercoagulable state and a fourfold increase in thrombosis risk, and chemotherapy increases this risk even more.³ Although tissue pathology examination is important for differentiating thrombosis from tumor, visualization of the direct extension of the mass from the primary source into the heart through the inferior vena cava by ultrasonography, computed tomography, or magnetic resonance imaging may help in making this distinction.²

To the Editor: We read with great interest the article by Patnaik et al¹ about a patient who had a cardiac metastasis of ovarian cancer, and we would like to raise a few points.

It is important to clarify that metastatic cardiac tumors are not necessary malignant. Intravenous leiomyomatosis is a benign small-muscle tumor that can spread to the heart, causing various cardiac symptoms.² Even with extensive disease, patients with intravenous leiomyomatosis may remain asymptomatic until cardiac involvement occurs. The most common cardiac symptoms are dyspnea, syncope, and lower-extremity edema.

Cardiac involvement in intravenous leiomyomatosis may occur via direct invasion or hematogenous or lymphatic spread of the tumor. In leiomyoma and leiomyosarcoma, cardiac invasion usually occurs via direct spread through the inferior vena cava into the right atrium and ventricle. Thus, cardiac involvement with these tumors (except for nephroma) was reported to exclusively involve the right side of the heart.

In 2014, we reported a unique case of intravenous leiomyomatosis that extended from the right side into the left side of the heart and the aorta via an atrial septal defect.² Intracardiac extension of intravenous leiomyomatosis may result in pulmonary embolism, systemic embolization if involving the left side, and, rarely, sudden death.²

In patients with malignancy, differentiating between thrombosis and tumor is critical. These patients have a hypercoagulable state and a fourfold increase in thrombosis risk, and chemotherapy increases this risk even more.³ Although tissue pathology examination is important for differentiating thrombosis from tumor, visualization of the direct extension of the mass from the primary source into the heart through the inferior vena cava by ultrasonography, computed tomography, or magnetic resonance imaging may help in making this distinction.²

To the Editor: As a geriatric medicine fellow, I eagerly read Hagerty and Rich’s review “Fall risk and anticoagulation for atrial fibrillation in the elderly: A delicate balance”¹ and Suh’s editorial, “Whether to anticoagulate: Toward a more reasoned approach”² in the January 2017 issue. Both pieces were helpful and informative.

I appreciate that Dr. Suh encourages shared decision-making between physicians and patients that balances patient preferences and risk stratification to inform whether to anticoagulate. He states, “Unfortunately, there is no similar screening tool to predict bleeding risk from anticoagulation with greater precision in the middle to lower part of the risk spectrum...The patient’s life expectancy and personal preferences are important independent factors that affect the decision of whether to anticoagulate or not.” 

Dr. Mark Eckman’s Atrial Fibrillation Decision Support Tool (AFDST) incorporates patients’ CHA₂DS₂-VASc and HAS-BLED scores to determine their quality-adjusted life expectancy on or off anticoagulation. The tool helps guide physicians and patients to make shared decisions about anticoagulation.^3–5 The AFDST informs clinicians if a patient is undertreated or being treated unnecessarily. Eckman and his colleagues have demonstrated the AFDST’s effective application in clinical practice, including for older adults. I invite readers to learn more about Eckman’s work!

To the Editor: As a geriatric medicine fellow, I eagerly read Hagerty and Rich’s review “Fall risk and anticoagulation for atrial fibrillation in the elderly: A delicate balance”¹ and Suh’s editorial, “Whether to anticoagulate: Toward a more reasoned approach”² in the January 2017 issue. Both pieces were helpful and informative.

I appreciate that Dr. Suh encourages shared decision-making between physicians and patients that balances patient preferences and risk stratification to inform whether to anticoagulate. He states, “Unfortunately, there is no similar screening tool to predict bleeding risk from anticoagulation with greater precision in the middle to lower part of the risk spectrum...The patient’s life expectancy and personal preferences are important independent factors that affect the decision of whether to anticoagulate or not.” 

Dr. Mark Eckman’s Atrial Fibrillation Decision Support Tool (AFDST) incorporates patients’ CHA₂DS₂-VASc and HAS-BLED scores to determine their quality-adjusted life expectancy on or off anticoagulation. The tool helps guide physicians and patients to make shared decisions about anticoagulation.^3–5 The AFDST informs clinicians if a patient is undertreated or being treated unnecessarily. Eckman and his colleagues have demonstrated the AFDST’s effective application in clinical practice, including for older adults. I invite readers to learn more about Eckman’s work!

To the Editor: As a geriatric medicine fellow, I eagerly read Hagerty and Rich’s review “Fall risk and anticoagulation for atrial fibrillation in the elderly: A delicate balance”¹ and Suh’s editorial, “Whether to anticoagulate: Toward a more reasoned approach”² in the January 2017 issue. Both pieces were helpful and informative.

I appreciate that Dr. Suh encourages shared decision-making between physicians and patients that balances patient preferences and risk stratification to inform whether to anticoagulate. He states, “Unfortunately, there is no similar screening tool to predict bleeding risk from anticoagulation with greater precision in the middle to lower part of the risk spectrum...The patient’s life expectancy and personal preferences are important independent factors that affect the decision of whether to anticoagulate or not.” 

Dr. Mark Eckman’s Atrial Fibrillation Decision Support Tool (AFDST) incorporates patients’ CHA₂DS₂-VASc and HAS-BLED scores to determine their quality-adjusted life expectancy on or off anticoagulation. The tool helps guide physicians and patients to make shared decisions about anticoagulation.^3–5 The AFDST informs clinicians if a patient is undertreated or being treated unnecessarily. Eckman and his colleagues have demonstrated the AFDST’s effective application in clinical practice, including for older adults. I invite readers to learn more about Eckman’s work!

In Reply: I appreciate Dr. Henning’s letter in response to my editorial.¹ Indeed, Dr. Eckman’s Atrial Fibrillation Decision Support Tool (AFDST) is useful for determining quality-adjusted life expectancy on or off anticoagulation, and could possibly help with shared decision-making in regard to anticoagulation.^2–4 

However, the AFDST does not incorporate personal preferences regarding anticoagulant or medication use in general. Many older adults are on too many medications (ie, polypharmacy) and wish to reduce their overall pill count.

A number of potential barriers to shared decision-making regarding medication use have been identified, including poor physician communication skills, the growing number of available medications, multiple prescribers for the same patient, lack of trust in the prescribing physician, and patients feeling that their preferences are not valued or important.⁵ Until communication and acceptance between prescribers and patients regarding possible medication choices improves, shared decision-making for medication use in general and anticoagulant use in particular will be an unfulfilled ideal.

In Reply: I appreciate Dr. Henning’s letter in response to my editorial.¹ Indeed, Dr. Eckman’s Atrial Fibrillation Decision Support Tool (AFDST) is useful for determining quality-adjusted life expectancy on or off anticoagulation, and could possibly help with shared decision-making in regard to anticoagulation.^2–4 

However, the AFDST does not incorporate personal preferences regarding anticoagulant or medication use in general. Many older adults are on too many medications (ie, polypharmacy) and wish to reduce their overall pill count.

A number of potential barriers to shared decision-making regarding medication use have been identified, including poor physician communication skills, the growing number of available medications, multiple prescribers for the same patient, lack of trust in the prescribing physician, and patients feeling that their preferences are not valued or important.⁵ Until communication and acceptance between prescribers and patients regarding possible medication choices improves, shared decision-making for medication use in general and anticoagulant use in particular will be an unfulfilled ideal.

In Reply: I appreciate Dr. Henning’s letter in response to my editorial.¹ Indeed, Dr. Eckman’s Atrial Fibrillation Decision Support Tool (AFDST) is useful for determining quality-adjusted life expectancy on or off anticoagulation, and could possibly help with shared decision-making in regard to anticoagulation.^2–4 

However, the AFDST does not incorporate personal preferences regarding anticoagulant or medication use in general. Many older adults are on too many medications (ie, polypharmacy) and wish to reduce their overall pill count.

A number of potential barriers to shared decision-making regarding medication use have been identified, including poor physician communication skills, the growing number of available medications, multiple prescribers for the same patient, lack of trust in the prescribing physician, and patients feeling that their preferences are not valued or important.⁵ Until communication and acceptance between prescribers and patients regarding possible medication choices improves, shared decision-making for medication use in general and anticoagulant use in particular will be an unfulfilled ideal.

Many patients, clinicians, and researchers had hoped that renal denervation would help control resistant hypertension. However, in the SYMPLICITY HTN-3 trial,¹ named for the catheter-based system used in the study (Symplicity RDN, Medtronic, Dublin, Ireland), this endovascular procedure failed to meet its primary and secondary efficacy end points, although it was found to be safe. These results were surprising, especially given the results of an earlier randomized trial (SYMPLICITY HTN-2),² which showed larger reductions in blood pressures 6 months after denervation than in the current trial.

See related editorial

Here, we discuss the results of the SYMPLICITY HTN-3 trial and offer possible explanations for its negative outcomes.

LEAD-UP TO SYMPLICITY HTN-3

Renal denervation consists of passing a catheter through the femoral artery into the renal arteries and ablating their sympathetic nerves using radiofrequency energy. In theory, this should interrupt efferent sympathetic communication between the brain and renal arteries, reducing muscular contraction of these arteries, increasing renal blood flow, reducing activation of the renin-angiotensin-adosterone system, thus reducing sodium retention, reducing afferent sympathetic communication between the kidneys and brain, and in turn reducing further sympathetic activity elsewhere in the body, such as in the heart. Blood pressure should fall.³

The results of the SYMPLICITY HTN-1 and 2 trials were discussed in an earlier article in this Journal,³ and the Medtronic-Ardian renal denervation system has been available in Europe and Australia for clinical use for over 2 years.⁴ Indeed, after the SYMPLICITY HTN-2 results were published in 2010, Boston Scientific’s Vessix, St. Jude Medical’s EnligHTN, and Covidien’s OneShot radiofrequency renal denervation devices—albeit each with some modifications—received a Conformité Européene (CE) mark and became available in Europe and Australia for clinical use. These devices are not available for clinical use or research in the United States.^3,5

Therefore, SYMPLICITY HTN-3, sponsored by Medtronic, was designed to obtain US Food and Drug Administration approval in the United States.⁶

SYMPLICITY HTN-3 DESIGN

Inclusion criteria were similar to those in the earlier SYMPLICITY trials. Patients had to have resistant hypertension, defined as a systolic blood pressure ≥ 160 mm Hg despite taking at least 3 blood pressure medications at maximum tolerated doses. Patients were excluded if they had a glomerular filtration rate of less than 45 mL/min/1.73 m², renal artery stenosis, or known secondary hypertension.

A total of 1,441 patients were enrolled, of whom 364 were eventually randomized to undergo renal denervation, and 171 were randomized to undergo a sham procedure. The mean systolic blood pressure at baseline was 188 mm Hg in each group. Most patients were taking maximum doses of blood pressure medications, and almost one-fourth were taking an aldosterone antagonist. Patients in both groups were taking an average of 5 medications.

The 2 groups were well matched for important covariates, including obstructive sleep apnea, diabetes mellitus, and renal insufficiency. Most of the patients were white; 25% of the renal denervation group and 29% of the sham procedure group were black.

The physicians conducting the follow-up appointments did not know which procedure the patients underwent, and neither did the patients. Medications were closely monitored, and patients had close follow-up. The catheter (Symplicity RDS, Medtronic) was of the same design that was used in the earlier SYMPLICITY trials and in clinical practice in countries where renal denervation was available.

Researchers expected that the systolic blood pressure, as measured in the office, would fall in both groups, but they hoped it would fall farther in the denervation group—at least 5 mm Hg farther, the primary end point of the trial. The secondary effectiveness end point was a 2-mm Hg greater reduction in 24-hour ambulatory systolic blood pressure.

No statistically significant difference in safety was observed between the denervation and control groups. However, the procedure was associated with 1 embolic event and 1 case of renal artery stenosis.

Blood pressure fell in both groups. However, at 6 months, office systolic pressure had fallen by a mean of 14.13 mm Hg in the denervation group and 11.74 mm Hg in the sham procedure group, a difference of only 2.39 mm Hg. The mean ambulatory systolic blood pressure had fallen by 6.75 vs 4.79 mm Hg, a difference of only 1.96 mm Hg. Neither difference was statistically significant.

A number of prespecified subgroup analyses were conducted, but the benefit of the procedure was statistically significant in only 3 subgroups: patients who were not black (P = .01), patients who were less than 65 years old (P = .04), and patients who had an estimated glomerular filtration rate of 60 mL/min/1.73 m² or higher (P = .05).

WHAT WENT WRONG?

The results of SYMPLICITY HTN-3 were disappointing and led companies that were developing renal denervation devices to discontinue or reevaluate their programs.

Although the results were surprising, many observers (including our group) raised concerns about the initial enthusiasm surrounding renal denervation.^3–7 Indeed, in 2010, we had concerns about the discrepancy between office-based blood pressure measurements (the primary end point of all renal denervation trials) and ambulatory blood pressure measurements in SYMPLICITY HTN-2.⁷

The enthusiasm surrounding this procedure led to the publication of 2 consensus documents on this novel therapy based on only 1 small randomized controlled study (SYMPLICITY HTN-2).^8,9 Renal denervation was even reported to be useful in other conditions involving the sympathorenal axis, including diabetes mellitus, metabolic syndrome, and obstructive sleep apnea, and also as a potential treatment adjunct in atrial fibrillation and other arrhythmias.⁵

What went wrong?

Shortcomings in trial design?

The trial was well designed. Both patients and operators were blinded to the procedure, and 24-hour ambulatory blood pressure monitoring was used. We presume that appropriate patients with resistant hypertension were enrolled—the mean baseline systolic blood pressure was 188 mm Hg, and patients in each group were taking an average of 5 medications.

On the other hand, true medication adherence is difficult to ascertain. Further, the term maximal “tolerated” doses of medications is vague, and we cannot rule out the possibility that some patients were enrolled who did not truly have resistant hypertension—they simply did not want to take medications.

Patients were required to be on a stable medication regimen before enrollment and, ideally, to not have any medication changes during the course of the study, but at least 40% of patients did require medication changes during the study. Additionally, it is unclear whether all patients underwent specific testing to rule out secondary hypertension, as this was done at the discretion of the treating physician.

First-generation catheters?

The same type of catheter was used as in the earlier SYMPLICITY trials, and it had been used in many patients in clinical practice in countries where the catheter is routinely available. It is unknown, however, whether newer multisite denervation devices would yield better results than the first-generation devices used in SYMPLICITY HTN-3. But even this would not explain the discrepancies in data between earlier trials and this trial.

Operator inexperience?

It has been suggested that operator inexperience may have played a role, but an analysis of operator volume did not find any association between this variable and the outcomes. Each procedure was supervised by at least 1 and in most cases 2 certified Medtronic representatives, who made certain that meticulous attention was paid to procedure details and that no shortcuts were taken during the procedure.

Inadequate ablation?

While we can assume that the correct technique was followed in most cases, renal denervation is still a “blind” procedure, and there is no nerve mapping to ascertain the degree of ablation achieved. Notably, patients who had the most ablations reportedly had a greater average drop in systolic ambulatory blood pressure than those who received fewer ablations. Sympathetic nervous system activity is a potential marker of adequacy of ablation, but it was not routinely assessed in the SYMPLICITY HTN-3 trial. Techniques to assess sympathetic nerve activity such as norepinephrine spillover and muscle sympathetic nerve activity are highly specialized and available only at a few research centers, and are not available for routine clinical use.

While these points may explain the negative findings of this trial, they fail to account for the discrepant results between this study and previous trials that used exactly the same definitions and techniques.

Is it possible that renal denervation has a differential effect according to race? All previous renal denervation studies were conducted in Europe or Australia; therefore, few data are available on the efficacy of the procedure in other racial groups, such as black Americans. Most of the patients in this trial were white, but approximately 25% were black—a good representation. There was a statistically significant benefit favoring renal denervation in nonblack (mostly white) patients, but not in black patients. This may be related to racial differences in the pathophysiology of hypertension or possibly due to chance alone.

A Hawthorne effect?

A Hawthorne effect (patients being more compliant because physicians are paying more attention to them) is unlikely, since the renal denervation arm did not have any reduction in blood pressure medications. At 6 months, both the sham group and the procedure group were still on an average of 5 medications.

Additionally, while the blood pressure reduction in both treatment groups was significant, the systolic blood pressure at 6 months was still 166 mm Hg in the denervation group and 168 mm Hg in the sham group. If denervation was effective, one would have expected a greater reduction in blood pressure or at least a decrease in the number of medications needed, eg, 1 to 2 fewer medications in the denervation group compared with the sham procedure group.

Regression to the mean?

It is unknown whether the results represent a statistical error such as regression to the mean. But given the run-in period and the confirmatory data from 24-hour ambulatory blood pressure, this would be unlikely.

WHAT NOW?

Is renal denervation dead? SYMPLICITY HTN-3 is only a single trial with multiple shortcomings and lessons to learn from. Since its publication, there have been updates from 2 prospective, randomized, open-label trials concerning the efficacy of catheter-based renal denervation in lowering blood pressure.^10,11

DENERHTN (Renal Denervation for Hypertension)¹⁰ studied patients with ambulatory systolic blood pressure higher than 135 mm Hg, diastolic blood pressure higher than 80 mm Hg, or both (after excluding secondary etiologies), despite 4 weeks of standardized triple-drug treatment including a diuretic. Patients were randomized to standardized stepped-care antihypertensive treatment alone (control group) or standard care plus renal denervation. The latter resulted in a significant further reduction in ambulatory blood pressure at 6 months.

The Prague-15 trial¹¹ studied patients with resistant hypertension. Secondary etiologies were excluded and adherence to therapy was confirmed by measuring plasma medication levels. It showed that renal denervation along with optimal antihypertensive medical therapy (unchanged after randomization) resulted in a significant reduction in ambulatory blood pressure that was comparable to the effect of intensified antihypertensive medical therapy including spironolactone. (Studies have shown that spironolactone is effective when added on as a fourth-line medication in resistant hypertension.¹²) At 6 months, patients in the intensive medical therapy group were using an average of 0.3 more antihypertensive medications than those in the procedure group.

These two trials addressed some of the drawbacks of the SYMPLICITY HTN-3 trial. However, both have many limitations including and not limited to being open-label and nonblinded, lacking a sham procedure, using a lower blood pressure threshold than SYMPLICITY HTN-3 did to define resistant hypertension, and using the same catheter as in the SYMPLICITY trials.

Advanced renal denervation catheters are needed that are multielectrode, smaller, easier to manipulate, and capable of providing simultaneous, circumferential, more-intense, and deeper ablations. The ongoing Investigator-Steered Project on Intravascular Renal Denervation for Management of Drug-Resistant Hypertension (INSPIRED)¹⁶ and Renal Denervation Using the Vessix Renal Denervation System for the Treatment of Hypertension (REDUCE-HTN: REINFORCE)¹⁷ trials are using contemporary innovative ablation catheters to address the limitations of the first-generation Symplicity catheter.

Further, Fischell et al¹⁸ reported encouraging results of renal denervation performed by injecting ethanol into the adventitial space of the renal arteries. This is still an invasive procedure; however, ethanol can spread out in all directions and reach all targeted nerves, potentially resulting in a more complete renal artery sympathetic ablation.

As technology advances, the WAVE IV trial¹⁹ is examining renal denervation performed from the outside through the skin using high-intensity focused ultrasound, which eliminates the need for femoral arterial catheterization, a promising noninvasive approach.

Proposals for future trials

The European Clinical Consensus Conference for Renal Denervation²⁰ proposed that future trials of renal denervation include patients with moderate rather than resistant hypertension, reflecting the pathogenic importance of sympathetic activity in earlier stages of hypertension. The conference also proposed excluding patients with stiff large arteries, a cause of isolated systolic hypertension. Other proposals included standardizing concomitant antihypertensive therapy, preferably treating all patients with the combination of a renin-angiotensin system blocker, calcium channel blocker, and diuretic in the run-in period; monitoring drug adherence through the use of pill counts, electronic pill dispensers, and drug blood tests; and using change in ambulatory blood pressure as the primary efficacy end point and change in office blood pressure as a secondary end point.

Trials ongoing

To possibly address the limitations posed by the SYMPLICITY HTN-3 trial and to answer other important questions, several sham-controlled clinical trials of renal denervation are currently being conducted:

• INSPiRED¹⁶
• REDUCE-HTN: REINFORCE¹⁷
• Spyral HTN-Off Med²¹
• Spyral HTN-On Med²¹
• Study of the ReCor Medical Paradise System in Clinical Hypertension (RADIANCE-HTN).²²

We hope these new studies can more clearly identify subsets of patients who would benefit from this technology, determine predictors of blood pressure reduction in such patients, and lead to newer devices that may provide more complete ablation.

Obviously, we also need better ways to identify the exact location of these sympathetic nerves within the renal artery and have a clearer sense of procedural success.

Until then, our colleagues in Europe and Australia continue to treat patients with this technology as we appropriately and patiently wait for level 1 clinical evidence of its efficacy.

Acknowledgments: We thank Kathryn Brock, BA, Editorial Services Manager, Heart and Vascular Institute, Cleveland Clinic, for her assistance in the preparation of this paper.

Many patients, clinicians, and researchers had hoped that renal denervation would help control resistant hypertension. However, in the SYMPLICITY HTN-3 trial,¹ named for the catheter-based system used in the study (Symplicity RDN, Medtronic, Dublin, Ireland), this endovascular procedure failed to meet its primary and secondary efficacy end points, although it was found to be safe. These results were surprising, especially given the results of an earlier randomized trial (SYMPLICITY HTN-2),² which showed larger reductions in blood pressures 6 months after denervation than in the current trial.

See related editorial

Here, we discuss the results of the SYMPLICITY HTN-3 trial and offer possible explanations for its negative outcomes.

LEAD-UP TO SYMPLICITY HTN-3

Renal denervation consists of passing a catheter through the femoral artery into the renal arteries and ablating their sympathetic nerves using radiofrequency energy. In theory, this should interrupt efferent sympathetic communication between the brain and renal arteries, reducing muscular contraction of these arteries, increasing renal blood flow, reducing activation of the renin-angiotensin-adosterone system, thus reducing sodium retention, reducing afferent sympathetic communication between the kidneys and brain, and in turn reducing further sympathetic activity elsewhere in the body, such as in the heart. Blood pressure should fall.³

The results of the SYMPLICITY HTN-1 and 2 trials were discussed in an earlier article in this Journal,³ and the Medtronic-Ardian renal denervation system has been available in Europe and Australia for clinical use for over 2 years.⁴ Indeed, after the SYMPLICITY HTN-2 results were published in 2010, Boston Scientific’s Vessix, St. Jude Medical’s EnligHTN, and Covidien’s OneShot radiofrequency renal denervation devices—albeit each with some modifications—received a Conformité Européene (CE) mark and became available in Europe and Australia for clinical use. These devices are not available for clinical use or research in the United States.^3,5

Therefore, SYMPLICITY HTN-3, sponsored by Medtronic, was designed to obtain US Food and Drug Administration approval in the United States.⁶

SYMPLICITY HTN-3 DESIGN

Inclusion criteria were similar to those in the earlier SYMPLICITY trials. Patients had to have resistant hypertension, defined as a systolic blood pressure ≥ 160 mm Hg despite taking at least 3 blood pressure medications at maximum tolerated doses. Patients were excluded if they had a glomerular filtration rate of less than 45 mL/min/1.73 m², renal artery stenosis, or known secondary hypertension.

A total of 1,441 patients were enrolled, of whom 364 were eventually randomized to undergo renal denervation, and 171 were randomized to undergo a sham procedure. The mean systolic blood pressure at baseline was 188 mm Hg in each group. Most patients were taking maximum doses of blood pressure medications, and almost one-fourth were taking an aldosterone antagonist. Patients in both groups were taking an average of 5 medications.

The 2 groups were well matched for important covariates, including obstructive sleep apnea, diabetes mellitus, and renal insufficiency. Most of the patients were white; 25% of the renal denervation group and 29% of the sham procedure group were black.

The physicians conducting the follow-up appointments did not know which procedure the patients underwent, and neither did the patients. Medications were closely monitored, and patients had close follow-up. The catheter (Symplicity RDS, Medtronic) was of the same design that was used in the earlier SYMPLICITY trials and in clinical practice in countries where renal denervation was available.

Researchers expected that the systolic blood pressure, as measured in the office, would fall in both groups, but they hoped it would fall farther in the denervation group—at least 5 mm Hg farther, the primary end point of the trial. The secondary effectiveness end point was a 2-mm Hg greater reduction in 24-hour ambulatory systolic blood pressure.

No statistically significant difference in safety was observed between the denervation and control groups. However, the procedure was associated with 1 embolic event and 1 case of renal artery stenosis.

Blood pressure fell in both groups. However, at 6 months, office systolic pressure had fallen by a mean of 14.13 mm Hg in the denervation group and 11.74 mm Hg in the sham procedure group, a difference of only 2.39 mm Hg. The mean ambulatory systolic blood pressure had fallen by 6.75 vs 4.79 mm Hg, a difference of only 1.96 mm Hg. Neither difference was statistically significant.

A number of prespecified subgroup analyses were conducted, but the benefit of the procedure was statistically significant in only 3 subgroups: patients who were not black (P = .01), patients who were less than 65 years old (P = .04), and patients who had an estimated glomerular filtration rate of 60 mL/min/1.73 m² or higher (P = .05).

WHAT WENT WRONG?

The results of SYMPLICITY HTN-3 were disappointing and led companies that were developing renal denervation devices to discontinue or reevaluate their programs.

Although the results were surprising, many observers (including our group) raised concerns about the initial enthusiasm surrounding renal denervation.^3–7 Indeed, in 2010, we had concerns about the discrepancy between office-based blood pressure measurements (the primary end point of all renal denervation trials) and ambulatory blood pressure measurements in SYMPLICITY HTN-2.⁷

The enthusiasm surrounding this procedure led to the publication of 2 consensus documents on this novel therapy based on only 1 small randomized controlled study (SYMPLICITY HTN-2).^8,9 Renal denervation was even reported to be useful in other conditions involving the sympathorenal axis, including diabetes mellitus, metabolic syndrome, and obstructive sleep apnea, and also as a potential treatment adjunct in atrial fibrillation and other arrhythmias.⁵

What went wrong?

Shortcomings in trial design?

The trial was well designed. Both patients and operators were blinded to the procedure, and 24-hour ambulatory blood pressure monitoring was used. We presume that appropriate patients with resistant hypertension were enrolled—the mean baseline systolic blood pressure was 188 mm Hg, and patients in each group were taking an average of 5 medications.

On the other hand, true medication adherence is difficult to ascertain. Further, the term maximal “tolerated” doses of medications is vague, and we cannot rule out the possibility that some patients were enrolled who did not truly have resistant hypertension—they simply did not want to take medications.

Patients were required to be on a stable medication regimen before enrollment and, ideally, to not have any medication changes during the course of the study, but at least 40% of patients did require medication changes during the study. Additionally, it is unclear whether all patients underwent specific testing to rule out secondary hypertension, as this was done at the discretion of the treating physician.

First-generation catheters?

The same type of catheter was used as in the earlier SYMPLICITY trials, and it had been used in many patients in clinical practice in countries where the catheter is routinely available. It is unknown, however, whether newer multisite denervation devices would yield better results than the first-generation devices used in SYMPLICITY HTN-3. But even this would not explain the discrepancies in data between earlier trials and this trial.

Operator inexperience?

It has been suggested that operator inexperience may have played a role, but an analysis of operator volume did not find any association between this variable and the outcomes. Each procedure was supervised by at least 1 and in most cases 2 certified Medtronic representatives, who made certain that meticulous attention was paid to procedure details and that no shortcuts were taken during the procedure.

Inadequate ablation?

While we can assume that the correct technique was followed in most cases, renal denervation is still a “blind” procedure, and there is no nerve mapping to ascertain the degree of ablation achieved. Notably, patients who had the most ablations reportedly had a greater average drop in systolic ambulatory blood pressure than those who received fewer ablations. Sympathetic nervous system activity is a potential marker of adequacy of ablation, but it was not routinely assessed in the SYMPLICITY HTN-3 trial. Techniques to assess sympathetic nerve activity such as norepinephrine spillover and muscle sympathetic nerve activity are highly specialized and available only at a few research centers, and are not available for routine clinical use.

While these points may explain the negative findings of this trial, they fail to account for the discrepant results between this study and previous trials that used exactly the same definitions and techniques.

Is it possible that renal denervation has a differential effect according to race? All previous renal denervation studies were conducted in Europe or Australia; therefore, few data are available on the efficacy of the procedure in other racial groups, such as black Americans. Most of the patients in this trial were white, but approximately 25% were black—a good representation. There was a statistically significant benefit favoring renal denervation in nonblack (mostly white) patients, but not in black patients. This may be related to racial differences in the pathophysiology of hypertension or possibly due to chance alone.

A Hawthorne effect?

A Hawthorne effect (patients being more compliant because physicians are paying more attention to them) is unlikely, since the renal denervation arm did not have any reduction in blood pressure medications. At 6 months, both the sham group and the procedure group were still on an average of 5 medications.

Additionally, while the blood pressure reduction in both treatment groups was significant, the systolic blood pressure at 6 months was still 166 mm Hg in the denervation group and 168 mm Hg in the sham group. If denervation was effective, one would have expected a greater reduction in blood pressure or at least a decrease in the number of medications needed, eg, 1 to 2 fewer medications in the denervation group compared with the sham procedure group.

Regression to the mean?

It is unknown whether the results represent a statistical error such as regression to the mean. But given the run-in period and the confirmatory data from 24-hour ambulatory blood pressure, this would be unlikely.

WHAT NOW?

Is renal denervation dead? SYMPLICITY HTN-3 is only a single trial with multiple shortcomings and lessons to learn from. Since its publication, there have been updates from 2 prospective, randomized, open-label trials concerning the efficacy of catheter-based renal denervation in lowering blood pressure.^10,11

DENERHTN (Renal Denervation for Hypertension)¹⁰ studied patients with ambulatory systolic blood pressure higher than 135 mm Hg, diastolic blood pressure higher than 80 mm Hg, or both (after excluding secondary etiologies), despite 4 weeks of standardized triple-drug treatment including a diuretic. Patients were randomized to standardized stepped-care antihypertensive treatment alone (control group) or standard care plus renal denervation. The latter resulted in a significant further reduction in ambulatory blood pressure at 6 months.

The Prague-15 trial¹¹ studied patients with resistant hypertension. Secondary etiologies were excluded and adherence to therapy was confirmed by measuring plasma medication levels. It showed that renal denervation along with optimal antihypertensive medical therapy (unchanged after randomization) resulted in a significant reduction in ambulatory blood pressure that was comparable to the effect of intensified antihypertensive medical therapy including spironolactone. (Studies have shown that spironolactone is effective when added on as a fourth-line medication in resistant hypertension.¹²) At 6 months, patients in the intensive medical therapy group were using an average of 0.3 more antihypertensive medications than those in the procedure group.

These two trials addressed some of the drawbacks of the SYMPLICITY HTN-3 trial. However, both have many limitations including and not limited to being open-label and nonblinded, lacking a sham procedure, using a lower blood pressure threshold than SYMPLICITY HTN-3 did to define resistant hypertension, and using the same catheter as in the SYMPLICITY trials.

Advanced renal denervation catheters are needed that are multielectrode, smaller, easier to manipulate, and capable of providing simultaneous, circumferential, more-intense, and deeper ablations. The ongoing Investigator-Steered Project on Intravascular Renal Denervation for Management of Drug-Resistant Hypertension (INSPIRED)¹⁶ and Renal Denervation Using the Vessix Renal Denervation System for the Treatment of Hypertension (REDUCE-HTN: REINFORCE)¹⁷ trials are using contemporary innovative ablation catheters to address the limitations of the first-generation Symplicity catheter.

Further, Fischell et al¹⁸ reported encouraging results of renal denervation performed by injecting ethanol into the adventitial space of the renal arteries. This is still an invasive procedure; however, ethanol can spread out in all directions and reach all targeted nerves, potentially resulting in a more complete renal artery sympathetic ablation.

As technology advances, the WAVE IV trial¹⁹ is examining renal denervation performed from the outside through the skin using high-intensity focused ultrasound, which eliminates the need for femoral arterial catheterization, a promising noninvasive approach.

Proposals for future trials

The European Clinical Consensus Conference for Renal Denervation²⁰ proposed that future trials of renal denervation include patients with moderate rather than resistant hypertension, reflecting the pathogenic importance of sympathetic activity in earlier stages of hypertension. The conference also proposed excluding patients with stiff large arteries, a cause of isolated systolic hypertension. Other proposals included standardizing concomitant antihypertensive therapy, preferably treating all patients with the combination of a renin-angiotensin system blocker, calcium channel blocker, and diuretic in the run-in period; monitoring drug adherence through the use of pill counts, electronic pill dispensers, and drug blood tests; and using change in ambulatory blood pressure as the primary efficacy end point and change in office blood pressure as a secondary end point.

Trials ongoing

To possibly address the limitations posed by the SYMPLICITY HTN-3 trial and to answer other important questions, several sham-controlled clinical trials of renal denervation are currently being conducted:

• INSPiRED¹⁶
• REDUCE-HTN: REINFORCE¹⁷
• Spyral HTN-Off Med²¹
• Spyral HTN-On Med²¹
• Study of the ReCor Medical Paradise System in Clinical Hypertension (RADIANCE-HTN).²²

We hope these new studies can more clearly identify subsets of patients who would benefit from this technology, determine predictors of blood pressure reduction in such patients, and lead to newer devices that may provide more complete ablation.

Obviously, we also need better ways to identify the exact location of these sympathetic nerves within the renal artery and have a clearer sense of procedural success.

Until then, our colleagues in Europe and Australia continue to treat patients with this technology as we appropriately and patiently wait for level 1 clinical evidence of its efficacy.

Acknowledgments: We thank Kathryn Brock, BA, Editorial Services Manager, Heart and Vascular Institute, Cleveland Clinic, for her assistance in the preparation of this paper.

Many patients, clinicians, and researchers had hoped that renal denervation would help control resistant hypertension. However, in the SYMPLICITY HTN-3 trial,¹ named for the catheter-based system used in the study (Symplicity RDN, Medtronic, Dublin, Ireland), this endovascular procedure failed to meet its primary and secondary efficacy end points, although it was found to be safe. These results were surprising, especially given the results of an earlier randomized trial (SYMPLICITY HTN-2),² which showed larger reductions in blood pressures 6 months after denervation than in the current trial.

See related editorial

Here, we discuss the results of the SYMPLICITY HTN-3 trial and offer possible explanations for its negative outcomes.

LEAD-UP TO SYMPLICITY HTN-3

Renal denervation consists of passing a catheter through the femoral artery into the renal arteries and ablating their sympathetic nerves using radiofrequency energy. In theory, this should interrupt efferent sympathetic communication between the brain and renal arteries, reducing muscular contraction of these arteries, increasing renal blood flow, reducing activation of the renin-angiotensin-adosterone system, thus reducing sodium retention, reducing afferent sympathetic communication between the kidneys and brain, and in turn reducing further sympathetic activity elsewhere in the body, such as in the heart. Blood pressure should fall.³

The results of the SYMPLICITY HTN-1 and 2 trials were discussed in an earlier article in this Journal,³ and the Medtronic-Ardian renal denervation system has been available in Europe and Australia for clinical use for over 2 years.⁴ Indeed, after the SYMPLICITY HTN-2 results were published in 2010, Boston Scientific’s Vessix, St. Jude Medical’s EnligHTN, and Covidien’s OneShot radiofrequency renal denervation devices—albeit each with some modifications—received a Conformité Européene (CE) mark and became available in Europe and Australia for clinical use. These devices are not available for clinical use or research in the United States.^3,5

Therefore, SYMPLICITY HTN-3, sponsored by Medtronic, was designed to obtain US Food and Drug Administration approval in the United States.⁶

SYMPLICITY HTN-3 DESIGN

Inclusion criteria were similar to those in the earlier SYMPLICITY trials. Patients had to have resistant hypertension, defined as a systolic blood pressure ≥ 160 mm Hg despite taking at least 3 blood pressure medications at maximum tolerated doses. Patients were excluded if they had a glomerular filtration rate of less than 45 mL/min/1.73 m², renal artery stenosis, or known secondary hypertension.

A total of 1,441 patients were enrolled, of whom 364 were eventually randomized to undergo renal denervation, and 171 were randomized to undergo a sham procedure. The mean systolic blood pressure at baseline was 188 mm Hg in each group. Most patients were taking maximum doses of blood pressure medications, and almost one-fourth were taking an aldosterone antagonist. Patients in both groups were taking an average of 5 medications.

The 2 groups were well matched for important covariates, including obstructive sleep apnea, diabetes mellitus, and renal insufficiency. Most of the patients were white; 25% of the renal denervation group and 29% of the sham procedure group were black.

The physicians conducting the follow-up appointments did not know which procedure the patients underwent, and neither did the patients. Medications were closely monitored, and patients had close follow-up. The catheter (Symplicity RDS, Medtronic) was of the same design that was used in the earlier SYMPLICITY trials and in clinical practice in countries where renal denervation was available.

Researchers expected that the systolic blood pressure, as measured in the office, would fall in both groups, but they hoped it would fall farther in the denervation group—at least 5 mm Hg farther, the primary end point of the trial. The secondary effectiveness end point was a 2-mm Hg greater reduction in 24-hour ambulatory systolic blood pressure.

No statistically significant difference in safety was observed between the denervation and control groups. However, the procedure was associated with 1 embolic event and 1 case of renal artery stenosis.

Blood pressure fell in both groups. However, at 6 months, office systolic pressure had fallen by a mean of 14.13 mm Hg in the denervation group and 11.74 mm Hg in the sham procedure group, a difference of only 2.39 mm Hg. The mean ambulatory systolic blood pressure had fallen by 6.75 vs 4.79 mm Hg, a difference of only 1.96 mm Hg. Neither difference was statistically significant.

A number of prespecified subgroup analyses were conducted, but the benefit of the procedure was statistically significant in only 3 subgroups: patients who were not black (P = .01), patients who were less than 65 years old (P = .04), and patients who had an estimated glomerular filtration rate of 60 mL/min/1.73 m² or higher (P = .05).

WHAT WENT WRONG?

The results of SYMPLICITY HTN-3 were disappointing and led companies that were developing renal denervation devices to discontinue or reevaluate their programs.

Although the results were surprising, many observers (including our group) raised concerns about the initial enthusiasm surrounding renal denervation.^3–7 Indeed, in 2010, we had concerns about the discrepancy between office-based blood pressure measurements (the primary end point of all renal denervation trials) and ambulatory blood pressure measurements in SYMPLICITY HTN-2.⁷

The enthusiasm surrounding this procedure led to the publication of 2 consensus documents on this novel therapy based on only 1 small randomized controlled study (SYMPLICITY HTN-2).^8,9 Renal denervation was even reported to be useful in other conditions involving the sympathorenal axis, including diabetes mellitus, metabolic syndrome, and obstructive sleep apnea, and also as a potential treatment adjunct in atrial fibrillation and other arrhythmias.⁵

What went wrong?

Shortcomings in trial design?

The trial was well designed. Both patients and operators were blinded to the procedure, and 24-hour ambulatory blood pressure monitoring was used. We presume that appropriate patients with resistant hypertension were enrolled—the mean baseline systolic blood pressure was 188 mm Hg, and patients in each group were taking an average of 5 medications.

On the other hand, true medication adherence is difficult to ascertain. Further, the term maximal “tolerated” doses of medications is vague, and we cannot rule out the possibility that some patients were enrolled who did not truly have resistant hypertension—they simply did not want to take medications.

Patients were required to be on a stable medication regimen before enrollment and, ideally, to not have any medication changes during the course of the study, but at least 40% of patients did require medication changes during the study. Additionally, it is unclear whether all patients underwent specific testing to rule out secondary hypertension, as this was done at the discretion of the treating physician.

First-generation catheters?

The same type of catheter was used as in the earlier SYMPLICITY trials, and it had been used in many patients in clinical practice in countries where the catheter is routinely available. It is unknown, however, whether newer multisite denervation devices would yield better results than the first-generation devices used in SYMPLICITY HTN-3. But even this would not explain the discrepancies in data between earlier trials and this trial.

Operator inexperience?

It has been suggested that operator inexperience may have played a role, but an analysis of operator volume did not find any association between this variable and the outcomes. Each procedure was supervised by at least 1 and in most cases 2 certified Medtronic representatives, who made certain that meticulous attention was paid to procedure details and that no shortcuts were taken during the procedure.

Inadequate ablation?

While we can assume that the correct technique was followed in most cases, renal denervation is still a “blind” procedure, and there is no nerve mapping to ascertain the degree of ablation achieved. Notably, patients who had the most ablations reportedly had a greater average drop in systolic ambulatory blood pressure than those who received fewer ablations. Sympathetic nervous system activity is a potential marker of adequacy of ablation, but it was not routinely assessed in the SYMPLICITY HTN-3 trial. Techniques to assess sympathetic nerve activity such as norepinephrine spillover and muscle sympathetic nerve activity are highly specialized and available only at a few research centers, and are not available for routine clinical use.

While these points may explain the negative findings of this trial, they fail to account for the discrepant results between this study and previous trials that used exactly the same definitions and techniques.

Is it possible that renal denervation has a differential effect according to race? All previous renal denervation studies were conducted in Europe or Australia; therefore, few data are available on the efficacy of the procedure in other racial groups, such as black Americans. Most of the patients in this trial were white, but approximately 25% were black—a good representation. There was a statistically significant benefit favoring renal denervation in nonblack (mostly white) patients, but not in black patients. This may be related to racial differences in the pathophysiology of hypertension or possibly due to chance alone.

A Hawthorne effect?

A Hawthorne effect (patients being more compliant because physicians are paying more attention to them) is unlikely, since the renal denervation arm did not have any reduction in blood pressure medications. At 6 months, both the sham group and the procedure group were still on an average of 5 medications.

Additionally, while the blood pressure reduction in both treatment groups was significant, the systolic blood pressure at 6 months was still 166 mm Hg in the denervation group and 168 mm Hg in the sham group. If denervation was effective, one would have expected a greater reduction in blood pressure or at least a decrease in the number of medications needed, eg, 1 to 2 fewer medications in the denervation group compared with the sham procedure group.

Regression to the mean?

It is unknown whether the results represent a statistical error such as regression to the mean. But given the run-in period and the confirmatory data from 24-hour ambulatory blood pressure, this would be unlikely.

WHAT NOW?

Is renal denervation dead? SYMPLICITY HTN-3 is only a single trial with multiple shortcomings and lessons to learn from. Since its publication, there have been updates from 2 prospective, randomized, open-label trials concerning the efficacy of catheter-based renal denervation in lowering blood pressure.^10,11

DENERHTN (Renal Denervation for Hypertension)¹⁰ studied patients with ambulatory systolic blood pressure higher than 135 mm Hg, diastolic blood pressure higher than 80 mm Hg, or both (after excluding secondary etiologies), despite 4 weeks of standardized triple-drug treatment including a diuretic. Patients were randomized to standardized stepped-care antihypertensive treatment alone (control group) or standard care plus renal denervation. The latter resulted in a significant further reduction in ambulatory blood pressure at 6 months.

The Prague-15 trial¹¹ studied patients with resistant hypertension. Secondary etiologies were excluded and adherence to therapy was confirmed by measuring plasma medication levels. It showed that renal denervation along with optimal antihypertensive medical therapy (unchanged after randomization) resulted in a significant reduction in ambulatory blood pressure that was comparable to the effect of intensified antihypertensive medical therapy including spironolactone. (Studies have shown that spironolactone is effective when added on as a fourth-line medication in resistant hypertension.¹²) At 6 months, patients in the intensive medical therapy group were using an average of 0.3 more antihypertensive medications than those in the procedure group.

These two trials addressed some of the drawbacks of the SYMPLICITY HTN-3 trial. However, both have many limitations including and not limited to being open-label and nonblinded, lacking a sham procedure, using a lower blood pressure threshold than SYMPLICITY HTN-3 did to define resistant hypertension, and using the same catheter as in the SYMPLICITY trials.

Advanced renal denervation catheters are needed that are multielectrode, smaller, easier to manipulate, and capable of providing simultaneous, circumferential, more-intense, and deeper ablations. The ongoing Investigator-Steered Project on Intravascular Renal Denervation for Management of Drug-Resistant Hypertension (INSPIRED)¹⁶ and Renal Denervation Using the Vessix Renal Denervation System for the Treatment of Hypertension (REDUCE-HTN: REINFORCE)¹⁷ trials are using contemporary innovative ablation catheters to address the limitations of the first-generation Symplicity catheter.

Further, Fischell et al¹⁸ reported encouraging results of renal denervation performed by injecting ethanol into the adventitial space of the renal arteries. This is still an invasive procedure; however, ethanol can spread out in all directions and reach all targeted nerves, potentially resulting in a more complete renal artery sympathetic ablation.

As technology advances, the WAVE IV trial¹⁹ is examining renal denervation performed from the outside through the skin using high-intensity focused ultrasound, which eliminates the need for femoral arterial catheterization, a promising noninvasive approach.

Proposals for future trials

The European Clinical Consensus Conference for Renal Denervation²⁰ proposed that future trials of renal denervation include patients with moderate rather than resistant hypertension, reflecting the pathogenic importance of sympathetic activity in earlier stages of hypertension. The conference also proposed excluding patients with stiff large arteries, a cause of isolated systolic hypertension. Other proposals included standardizing concomitant antihypertensive therapy, preferably treating all patients with the combination of a renin-angiotensin system blocker, calcium channel blocker, and diuretic in the run-in period; monitoring drug adherence through the use of pill counts, electronic pill dispensers, and drug blood tests; and using change in ambulatory blood pressure as the primary efficacy end point and change in office blood pressure as a secondary end point.

Trials ongoing

To possibly address the limitations posed by the SYMPLICITY HTN-3 trial and to answer other important questions, several sham-controlled clinical trials of renal denervation are currently being conducted:

• INSPiRED¹⁶
• REDUCE-HTN: REINFORCE¹⁷
• Spyral HTN-Off Med²¹
• Spyral HTN-On Med²¹
• Study of the ReCor Medical Paradise System in Clinical Hypertension (RADIANCE-HTN).²²

We hope these new studies can more clearly identify subsets of patients who would benefit from this technology, determine predictors of blood pressure reduction in such patients, and lead to newer devices that may provide more complete ablation.

Obviously, we also need better ways to identify the exact location of these sympathetic nerves within the renal artery and have a clearer sense of procedural success.

Until then, our colleagues in Europe and Australia continue to treat patients with this technology as we appropriately and patiently wait for level 1 clinical evidence of its efficacy.

Acknowledgments: We thank Kathryn Brock, BA, Editorial Services Manager, Heart and Vascular Institute, Cleveland Clinic, for her assistance in the preparation of this paper.

When renal sympathetic denervation, an endovascular procedure designed to treat resistant hypertension, failed to meet its efficacy goal in the SYMPLICITY HTN-3 trial,¹ the news was disappointing.

See related article

In this issue of the Cleveland Clinic Journal of Medicine, Shishehbor et al² provide a critical review of the findings of that trial and summarize its intricacies, as well as the results of other important trials of renal denervation therapy for hypertension. To their excellent observations, we would like to add some of our own.

HYPERTENSION: COMMON, OFTEN RESISTANT

The worldwide prevalence of hypertension is increasing. In the year 2000, about 26% of the adult world population had hypertension; by the year 2025, the number is projected to rise to 29%—1.56 billion people.³

Only about 50% of patients with hypertension are treated for it and, of those, about half have it adequately controlled. In one report, about 30% of US patients with hypertension had adequate blood pressure control.⁴

Patients who have uncontrolled hypertension are usually older and more obese, have higher baseline blood pressure and excessive salt intake, and are more likely to have chronic kidney disease, diabetes, obstructive sleep apnea, and aldosterone excess.⁵ Many of these conditions are also associated with increased sympathetic nervous system activity.⁶

Resistance and pseudoresistance

But lack of control of blood pressure is not the same as resistant hypertension. It is important to differentiate resistant hypertension from pseudoresistant hypertension, ie, hypertension that only seems to be resistant.⁷ Resistant hypertension affects 12.8% of all drug-treated hypertensive patients in the United States, according to data from the National Health and Nutrition Examination Survey.⁸

Factors that can cause pseudoresistant hypertension include:

Suboptimal antihypertensive regimens (truly resistant hypertension means blood pressure that remains high despite concurrent treatment with 3 antihypertensive drugs of different classes, 1 of which is a diuretic, in maximal doses)

The white coat effect (higher blood pressure in the office than at home, presumably due to the stress of an office visit)

• Suboptimal blood pressure measurement techniques (eg, use of a cuff that is too small, causing falsely high readings)
• Physician inertia (eg, failure to change a regimen that is not working)
• Lifestyle factors (eg, excessive sodium intake)
• Medications that interfere with blood pressure control (eg, nonsteroidal anti-inflammatory drugs)
• Poor adherence to prescribed medications.

Causes of secondary hypertension such as obstructive sleep apnea, primary aldosteronism, and renal artery stenosis should also be ruled out before concluding that a patient has resistant hypertension.

Hypertension causes a myriad of medical diseases, including accelerated atherosclerosis, myocardial ischemia and infarction, both systolic and diastolic heart failure, rhythm problems (eg, atrial fibrillation), and stroke.

Most patients with resistant hypertension have no identifiable reversible causes of it, exhibit increased sympathetic nervous system activity, and have increased risk of cardiovascular events. The risk can be reduced by treatment.^9,10

Adequate and sustained treatment of hypertension prevents and mitigates its complications. The classic Veterans Administration Cooperative Study in the 1960s demonstrated a 96% reduction in cardiovascular events over 18 months with the use of 3 antihypertensive medications in patients with severe hypertension.¹¹ A reduction of as little as 2 mm Hg in the mean blood pressure has been associated with a 10% reduction in the risk of stroke mortality and a 7% decrease in ischemic heart disease mortality.¹² This is an important consideration when evaluating the clinical end points of hypertension trials.

SYMPLICITY HTN-3 TRIAL: WHAT DID WE LEARN?

As controlling blood pressure is paramount in reducing cardiovascular complications, it is only natural to look for innovative strategies to supplement the medical treatments of hypertension.

The multicenter SYMPLICITY HTN-3 trial¹ was undertaken to establish the efficacy of renal-artery denervation using radiofrequency energy delivered by a catheter-based system (Symplicity RDN, Medtronic, Dublin, Ireland). This randomized, sham-controlled, blinded study did not show a benefit from this procedure with respect to either of its efficacy end points—at 6 months, a reduction in office systolic blood pressure of at least 5 mm Hg more than with medical therapy alone, or a reduction in mean ambulatory systolic pressure of at least 2 mm Hg more than with medical therapy alone.

Despite the negative results, this medium-size (N = 535) randomized clinical trial still represents the highest-level evidence in the field, and we ought to learn something from it.

Limitations of SYMPLICITY HTN-3

Several factors may have contributed to the negative results of the trial. 

Patient selection. For the most part, patients enrolled in renal denervation trials, including SYMPLICITY HTN-3, were not selected on the basis of heightened sympathetic nervous system activity. Assessment of sympathetic nervous system activity may identify the population most likely to achieve an adequate response.

Of note, the baseline blood pressure readings of patients in this trial were higher in the office than on ambulatory monitoring. Patients with white coat hypertension have increased sympathetic nervous system activity and thus might actually be good candidates for renal denervation therapy.

Adequacy of ablation was not measured. Many argue that an objective measure of the adequacy of the denervation procedure (qualitative or quantitative) should have been implemented and, if it had been, the results might have been different. For example, when ablation is performed in the main renal artery as well as the branches, the efficacy in reducing levels of norepinephrine is improved.¹³

Blood pressure fell in both groups. In SYMPLICITY HTN-3 and many other renal denervation trials, patients were assessed using both office and ambulatory blood pressure measurements. The primary end point was the office blood pressure measurement, with a 5-mm Hg difference in reduction chosen to define the superiority margin. This margin was chosen because even small reductions in blood pressure are known to decrease adverse events caused by hypertension. Notably, blood pressure fell significantly in both the control and intervention groups, with an intergroup difference of 2.39 mm Hg (not statistically significant) in favor of denervation.

Medication questions. The SYMPLICITY HTN-3 patients were supposed to be on stable medical regimens with maximal tolerated doses before the procedure. However, it was difficult to assess patients’ adherence to and tolerance of medical therapies. Many (about 40%) of the patients had their medications changed during the study.¹

Therefore, a critical look at the study enrollment criteria may shed more light on the reasons for the negative findings. Did these patients truly have resistant hypertension? Before they underwent the treatment, was their prestudy pharmacologic regimen adequately intensified?

After the findings of the SYMPLICITY HTN-3 study were released, several other trials—such as the Renal Denervation for Hypertension (DENERHTN)¹⁴ and Prague-15 trials¹⁵—reported conflicting results. Notably, these were not sham-controlled trials.

Newer studies with robust trial designs are ongoing. A quick search of www.clinicaltrials.gov reveals that at least 89 active clinical trials of renal denervation are registered as of the date of this writing. Excluding those with unknown status, there are 63 trials open or ongoing.

Clinical trials are also ongoing to determine the effects of renal denervation in patients with heart failure, atrial fibrillation, sleep apnea, and chronic kidney disease, all of which are known to involve heightened sympathetic nervous system activity.

NOT READY FOR CLINICAL USE

Although nonpharmacologic treatments of hypertension continue to be studied and are supported by an avalanche of trials in animals and small, mostly nonrandomized trials in humans, one should not forget that the SYMPLICITY HTN-3 trial simply did not meet its primary efficacy end points. We need definitive clinical evidence showing that renal denervation reduces either blood pressure or clinical events before it becomes a mainstream therapy in humans.

Additional trials are being conducted that were designed in accordance with the recommendations of the European Clinical Consensus Conference for Renal Denervation¹⁶ in terms of study population, design, and end points. Well-designed studies that conform to those recommendations are critical.

Finally, although our enthusiasm for renal denervation as a treatment of hypertension is tempered, there have been no noteworthy safety concerns related to the procedure, which certainly helps maintain the research momentum in this field.              

When renal sympathetic denervation, an endovascular procedure designed to treat resistant hypertension, failed to meet its efficacy goal in the SYMPLICITY HTN-3 trial,¹ the news was disappointing.

See related article

In this issue of the Cleveland Clinic Journal of Medicine, Shishehbor et al² provide a critical review of the findings of that trial and summarize its intricacies, as well as the results of other important trials of renal denervation therapy for hypertension. To their excellent observations, we would like to add some of our own.

HYPERTENSION: COMMON, OFTEN RESISTANT

The worldwide prevalence of hypertension is increasing. In the year 2000, about 26% of the adult world population had hypertension; by the year 2025, the number is projected to rise to 29%—1.56 billion people.³

Only about 50% of patients with hypertension are treated for it and, of those, about half have it adequately controlled. In one report, about 30% of US patients with hypertension had adequate blood pressure control.⁴

Patients who have uncontrolled hypertension are usually older and more obese, have higher baseline blood pressure and excessive salt intake, and are more likely to have chronic kidney disease, diabetes, obstructive sleep apnea, and aldosterone excess.⁵ Many of these conditions are also associated with increased sympathetic nervous system activity.⁶

Resistance and pseudoresistance

But lack of control of blood pressure is not the same as resistant hypertension. It is important to differentiate resistant hypertension from pseudoresistant hypertension, ie, hypertension that only seems to be resistant.⁷ Resistant hypertension affects 12.8% of all drug-treated hypertensive patients in the United States, according to data from the National Health and Nutrition Examination Survey.⁸

Factors that can cause pseudoresistant hypertension include:

Suboptimal antihypertensive regimens (truly resistant hypertension means blood pressure that remains high despite concurrent treatment with 3 antihypertensive drugs of different classes, 1 of which is a diuretic, in maximal doses)

The white coat effect (higher blood pressure in the office than at home, presumably due to the stress of an office visit)

• Suboptimal blood pressure measurement techniques (eg, use of a cuff that is too small, causing falsely high readings)
• Physician inertia (eg, failure to change a regimen that is not working)
• Lifestyle factors (eg, excessive sodium intake)
• Medications that interfere with blood pressure control (eg, nonsteroidal anti-inflammatory drugs)
• Poor adherence to prescribed medications.

Causes of secondary hypertension such as obstructive sleep apnea, primary aldosteronism, and renal artery stenosis should also be ruled out before concluding that a patient has resistant hypertension.

Hypertension causes a myriad of medical diseases, including accelerated atherosclerosis, myocardial ischemia and infarction, both systolic and diastolic heart failure, rhythm problems (eg, atrial fibrillation), and stroke.

Most patients with resistant hypertension have no identifiable reversible causes of it, exhibit increased sympathetic nervous system activity, and have increased risk of cardiovascular events. The risk can be reduced by treatment.^9,10

Adequate and sustained treatment of hypertension prevents and mitigates its complications. The classic Veterans Administration Cooperative Study in the 1960s demonstrated a 96% reduction in cardiovascular events over 18 months with the use of 3 antihypertensive medications in patients with severe hypertension.¹¹ A reduction of as little as 2 mm Hg in the mean blood pressure has been associated with a 10% reduction in the risk of stroke mortality and a 7% decrease in ischemic heart disease mortality.¹² This is an important consideration when evaluating the clinical end points of hypertension trials.

SYMPLICITY HTN-3 TRIAL: WHAT DID WE LEARN?

As controlling blood pressure is paramount in reducing cardiovascular complications, it is only natural to look for innovative strategies to supplement the medical treatments of hypertension.

The multicenter SYMPLICITY HTN-3 trial¹ was undertaken to establish the efficacy of renal-artery denervation using radiofrequency energy delivered by a catheter-based system (Symplicity RDN, Medtronic, Dublin, Ireland). This randomized, sham-controlled, blinded study did not show a benefit from this procedure with respect to either of its efficacy end points—at 6 months, a reduction in office systolic blood pressure of at least 5 mm Hg more than with medical therapy alone, or a reduction in mean ambulatory systolic pressure of at least 2 mm Hg more than with medical therapy alone.

Despite the negative results, this medium-size (N = 535) randomized clinical trial still represents the highest-level evidence in the field, and we ought to learn something from it.

Limitations of SYMPLICITY HTN-3

Several factors may have contributed to the negative results of the trial. 

Patient selection. For the most part, patients enrolled in renal denervation trials, including SYMPLICITY HTN-3, were not selected on the basis of heightened sympathetic nervous system activity. Assessment of sympathetic nervous system activity may identify the population most likely to achieve an adequate response.

Of note, the baseline blood pressure readings of patients in this trial were higher in the office than on ambulatory monitoring. Patients with white coat hypertension have increased sympathetic nervous system activity and thus might actually be good candidates for renal denervation therapy.

Adequacy of ablation was not measured. Many argue that an objective measure of the adequacy of the denervation procedure (qualitative or quantitative) should have been implemented and, if it had been, the results might have been different. For example, when ablation is performed in the main renal artery as well as the branches, the efficacy in reducing levels of norepinephrine is improved.¹³

Blood pressure fell in both groups. In SYMPLICITY HTN-3 and many other renal denervation trials, patients were assessed using both office and ambulatory blood pressure measurements. The primary end point was the office blood pressure measurement, with a 5-mm Hg difference in reduction chosen to define the superiority margin. This margin was chosen because even small reductions in blood pressure are known to decrease adverse events caused by hypertension. Notably, blood pressure fell significantly in both the control and intervention groups, with an intergroup difference of 2.39 mm Hg (not statistically significant) in favor of denervation.

Medication questions. The SYMPLICITY HTN-3 patients were supposed to be on stable medical regimens with maximal tolerated doses before the procedure. However, it was difficult to assess patients’ adherence to and tolerance of medical therapies. Many (about 40%) of the patients had their medications changed during the study.¹

Therefore, a critical look at the study enrollment criteria may shed more light on the reasons for the negative findings. Did these patients truly have resistant hypertension? Before they underwent the treatment, was their prestudy pharmacologic regimen adequately intensified?

After the findings of the SYMPLICITY HTN-3 study were released, several other trials—such as the Renal Denervation for Hypertension (DENERHTN)¹⁴ and Prague-15 trials¹⁵—reported conflicting results. Notably, these were not sham-controlled trials.

Newer studies with robust trial designs are ongoing. A quick search of www.clinicaltrials.gov reveals that at least 89 active clinical trials of renal denervation are registered as of the date of this writing. Excluding those with unknown status, there are 63 trials open or ongoing.

Clinical trials are also ongoing to determine the effects of renal denervation in patients with heart failure, atrial fibrillation, sleep apnea, and chronic kidney disease, all of which are known to involve heightened sympathetic nervous system activity.

NOT READY FOR CLINICAL USE

Although nonpharmacologic treatments of hypertension continue to be studied and are supported by an avalanche of trials in animals and small, mostly nonrandomized trials in humans, one should not forget that the SYMPLICITY HTN-3 trial simply did not meet its primary efficacy end points. We need definitive clinical evidence showing that renal denervation reduces either blood pressure or clinical events before it becomes a mainstream therapy in humans.

Additional trials are being conducted that were designed in accordance with the recommendations of the European Clinical Consensus Conference for Renal Denervation¹⁶ in terms of study population, design, and end points. Well-designed studies that conform to those recommendations are critical.

Finally, although our enthusiasm for renal denervation as a treatment of hypertension is tempered, there have been no noteworthy safety concerns related to the procedure, which certainly helps maintain the research momentum in this field.              

When renal sympathetic denervation, an endovascular procedure designed to treat resistant hypertension, failed to meet its efficacy goal in the SYMPLICITY HTN-3 trial,¹ the news was disappointing.

See related article

In this issue of the Cleveland Clinic Journal of Medicine, Shishehbor et al² provide a critical review of the findings of that trial and summarize its intricacies, as well as the results of other important trials of renal denervation therapy for hypertension. To their excellent observations, we would like to add some of our own.

HYPERTENSION: COMMON, OFTEN RESISTANT

The worldwide prevalence of hypertension is increasing. In the year 2000, about 26% of the adult world population had hypertension; by the year 2025, the number is projected to rise to 29%—1.56 billion people.³

Only about 50% of patients with hypertension are treated for it and, of those, about half have it adequately controlled. In one report, about 30% of US patients with hypertension had adequate blood pressure control.⁴

Patients who have uncontrolled hypertension are usually older and more obese, have higher baseline blood pressure and excessive salt intake, and are more likely to have chronic kidney disease, diabetes, obstructive sleep apnea, and aldosterone excess.⁵ Many of these conditions are also associated with increased sympathetic nervous system activity.⁶

Resistance and pseudoresistance

But lack of control of blood pressure is not the same as resistant hypertension. It is important to differentiate resistant hypertension from pseudoresistant hypertension, ie, hypertension that only seems to be resistant.⁷ Resistant hypertension affects 12.8% of all drug-treated hypertensive patients in the United States, according to data from the National Health and Nutrition Examination Survey.⁸

Factors that can cause pseudoresistant hypertension include:

Suboptimal antihypertensive regimens (truly resistant hypertension means blood pressure that remains high despite concurrent treatment with 3 antihypertensive drugs of different classes, 1 of which is a diuretic, in maximal doses)

The white coat effect (higher blood pressure in the office than at home, presumably due to the stress of an office visit)

• Suboptimal blood pressure measurement techniques (eg, use of a cuff that is too small, causing falsely high readings)
• Physician inertia (eg, failure to change a regimen that is not working)
• Lifestyle factors (eg, excessive sodium intake)
• Medications that interfere with blood pressure control (eg, nonsteroidal anti-inflammatory drugs)
• Poor adherence to prescribed medications.

Causes of secondary hypertension such as obstructive sleep apnea, primary aldosteronism, and renal artery stenosis should also be ruled out before concluding that a patient has resistant hypertension.

Hypertension causes a myriad of medical diseases, including accelerated atherosclerosis, myocardial ischemia and infarction, both systolic and diastolic heart failure, rhythm problems (eg, atrial fibrillation), and stroke.

Most patients with resistant hypertension have no identifiable reversible causes of it, exhibit increased sympathetic nervous system activity, and have increased risk of cardiovascular events. The risk can be reduced by treatment.^9,10

Adequate and sustained treatment of hypertension prevents and mitigates its complications. The classic Veterans Administration Cooperative Study in the 1960s demonstrated a 96% reduction in cardiovascular events over 18 months with the use of 3 antihypertensive medications in patients with severe hypertension.¹¹ A reduction of as little as 2 mm Hg in the mean blood pressure has been associated with a 10% reduction in the risk of stroke mortality and a 7% decrease in ischemic heart disease mortality.¹² This is an important consideration when evaluating the clinical end points of hypertension trials.

SYMPLICITY HTN-3 TRIAL: WHAT DID WE LEARN?

As controlling blood pressure is paramount in reducing cardiovascular complications, it is only natural to look for innovative strategies to supplement the medical treatments of hypertension.

The multicenter SYMPLICITY HTN-3 trial¹ was undertaken to establish the efficacy of renal-artery denervation using radiofrequency energy delivered by a catheter-based system (Symplicity RDN, Medtronic, Dublin, Ireland). This randomized, sham-controlled, blinded study did not show a benefit from this procedure with respect to either of its efficacy end points—at 6 months, a reduction in office systolic blood pressure of at least 5 mm Hg more than with medical therapy alone, or a reduction in mean ambulatory systolic pressure of at least 2 mm Hg more than with medical therapy alone.

Despite the negative results, this medium-size (N = 535) randomized clinical trial still represents the highest-level evidence in the field, and we ought to learn something from it.

Limitations of SYMPLICITY HTN-3

Several factors may have contributed to the negative results of the trial. 

Patient selection. For the most part, patients enrolled in renal denervation trials, including SYMPLICITY HTN-3, were not selected on the basis of heightened sympathetic nervous system activity. Assessment of sympathetic nervous system activity may identify the population most likely to achieve an adequate response.

Of note, the baseline blood pressure readings of patients in this trial were higher in the office than on ambulatory monitoring. Patients with white coat hypertension have increased sympathetic nervous system activity and thus might actually be good candidates for renal denervation therapy.

Adequacy of ablation was not measured. Many argue that an objective measure of the adequacy of the denervation procedure (qualitative or quantitative) should have been implemented and, if it had been, the results might have been different. For example, when ablation is performed in the main renal artery as well as the branches, the efficacy in reducing levels of norepinephrine is improved.¹³

Blood pressure fell in both groups. In SYMPLICITY HTN-3 and many other renal denervation trials, patients were assessed using both office and ambulatory blood pressure measurements. The primary end point was the office blood pressure measurement, with a 5-mm Hg difference in reduction chosen to define the superiority margin. This margin was chosen because even small reductions in blood pressure are known to decrease adverse events caused by hypertension. Notably, blood pressure fell significantly in both the control and intervention groups, with an intergroup difference of 2.39 mm Hg (not statistically significant) in favor of denervation.

Medication questions. The SYMPLICITY HTN-3 patients were supposed to be on stable medical regimens with maximal tolerated doses before the procedure. However, it was difficult to assess patients’ adherence to and tolerance of medical therapies. Many (about 40%) of the patients had their medications changed during the study.¹

Therefore, a critical look at the study enrollment criteria may shed more light on the reasons for the negative findings. Did these patients truly have resistant hypertension? Before they underwent the treatment, was their prestudy pharmacologic regimen adequately intensified?

After the findings of the SYMPLICITY HTN-3 study were released, several other trials—such as the Renal Denervation for Hypertension (DENERHTN)¹⁴ and Prague-15 trials¹⁵—reported conflicting results. Notably, these were not sham-controlled trials.

Newer studies with robust trial designs are ongoing. A quick search of www.clinicaltrials.gov reveals that at least 89 active clinical trials of renal denervation are registered as of the date of this writing. Excluding those with unknown status, there are 63 trials open or ongoing.

Clinical trials are also ongoing to determine the effects of renal denervation in patients with heart failure, atrial fibrillation, sleep apnea, and chronic kidney disease, all of which are known to involve heightened sympathetic nervous system activity.

NOT READY FOR CLINICAL USE

Although nonpharmacologic treatments of hypertension continue to be studied and are supported by an avalanche of trials in animals and small, mostly nonrandomized trials in humans, one should not forget that the SYMPLICITY HTN-3 trial simply did not meet its primary efficacy end points. We need definitive clinical evidence showing that renal denervation reduces either blood pressure or clinical events before it becomes a mainstream therapy in humans.

Additional trials are being conducted that were designed in accordance with the recommendations of the European Clinical Consensus Conference for Renal Denervation¹⁶ in terms of study population, design, and end points. Well-designed studies that conform to those recommendations are critical.

Finally, although our enthusiasm for renal denervation as a treatment of hypertension is tempered, there have been no noteworthy safety concerns related to the procedure, which certainly helps maintain the research momentum in this field.              

Supplement Editor:
Aanchal Kapoor, MD

Contents

Introduction: Biostatistics and epidemiology lecture series, part 1
Aanchal Kapoor, MD

The architecture of clinical research
James K. Stoller

Basics of study design: Practical considerations
Robert L. Chatburn

Chi-square and Fisher's exact tests
Amy Nowacki

Supplement Editor:
Aanchal Kapoor, MD

Contents

Introduction: Biostatistics and epidemiology lecture series, part 1
Aanchal Kapoor, MD

The architecture of clinical research
James K. Stoller

Basics of study design: Practical considerations
Robert L. Chatburn

Chi-square and Fisher's exact tests
Amy Nowacki

Supplement Editor:
Aanchal Kapoor, MD

Contents

Introduction: Biostatistics and epidemiology lecture series, part 1
Aanchal Kapoor, MD

The architecture of clinical research
James K. Stoller

Basics of study design: Practical considerations
Robert L. Chatburn

Chi-square and Fisher's exact tests
Amy Nowacki

Physicians are inundated with clinical research findings that potentially impact patient care. Evaluating the strength and clinical application of research results requires an understanding of the underlying biostatistics and epidemiological principles.

The articles in this supplement are based on a series of lectures originally developed for fellows in pulmonary and critical care medicine to provide them with the tools to transform a scientific or clinical question into research projects, and then pursue the answer to their question with the appropriate methods. The same skills also enable them to appraise the published literature in a systematic and rigorous manner. 

Each topic in the series began with a presentation and discussion of statistical principles and methods, then moved to a practical module using the principles to appraise a specific publication. Participants in the course had an immediate opportunity to try the techniques, both to demonstrate understanding and to reinforce the concepts to each learner. The articles of this series follow the same outline, providing clinicians of all specialties the basic statistical tools to conduct and appraise clinical research, along with a sample article for practicing each statistical method presented.

This Cleveland Clinic Journal of Medicine supplement includes 3 lectures from the “Biostatistics and Epidemiology Lecture Series.” Dr. Stoller’s presentation, The Architecture of Clinical Research, describes the basic structure of clinical research and the nomenclature to understand trial design and sources of bias.

Building on those concepts, Dr. Chatburn’s lecture, Basics of Study Design: Practical Considerations, outlines the structured approach to develop a formal research protocol. How to identify a problem, expand the scope of it through a literature review, create a hypothesis, design a study, and an introduction to basic statistical methods are discussed.

And in Chi-square and Fisher’s Exact Tests, Dr. Nowacki introduces the statistical methodology of these 2 tests to assess associations between 2 independent categorical variables. The sample article illustrates step-by-step calculation of both the large sample approximation (chi-square) and exact (Fisher’s) methodologies providing insight into how these tests are conducted.

My hope is that these articles, and future installments based on forthcoming lectures, are helpful to physicians both in conducting their own research and in evaluating the research of others

Physicians are inundated with clinical research findings that potentially impact patient care. Evaluating the strength and clinical application of research results requires an understanding of the underlying biostatistics and epidemiological principles.

The articles in this supplement are based on a series of lectures originally developed for fellows in pulmonary and critical care medicine to provide them with the tools to transform a scientific or clinical question into research projects, and then pursue the answer to their question with the appropriate methods. The same skills also enable them to appraise the published literature in a systematic and rigorous manner. 

Each topic in the series began with a presentation and discussion of statistical principles and methods, then moved to a practical module using the principles to appraise a specific publication. Participants in the course had an immediate opportunity to try the techniques, both to demonstrate understanding and to reinforce the concepts to each learner. The articles of this series follow the same outline, providing clinicians of all specialties the basic statistical tools to conduct and appraise clinical research, along with a sample article for practicing each statistical method presented.

This Cleveland Clinic Journal of Medicine supplement includes 3 lectures from the “Biostatistics and Epidemiology Lecture Series.” Dr. Stoller’s presentation, The Architecture of Clinical Research, describes the basic structure of clinical research and the nomenclature to understand trial design and sources of bias.

Building on those concepts, Dr. Chatburn’s lecture, Basics of Study Design: Practical Considerations, outlines the structured approach to develop a formal research protocol. How to identify a problem, expand the scope of it through a literature review, create a hypothesis, design a study, and an introduction to basic statistical methods are discussed.

And in Chi-square and Fisher’s Exact Tests, Dr. Nowacki introduces the statistical methodology of these 2 tests to assess associations between 2 independent categorical variables. The sample article illustrates step-by-step calculation of both the large sample approximation (chi-square) and exact (Fisher’s) methodologies providing insight into how these tests are conducted.

My hope is that these articles, and future installments based on forthcoming lectures, are helpful to physicians both in conducting their own research and in evaluating the research of others

Physicians are inundated with clinical research findings that potentially impact patient care. Evaluating the strength and clinical application of research results requires an understanding of the underlying biostatistics and epidemiological principles.

The articles in this supplement are based on a series of lectures originally developed for fellows in pulmonary and critical care medicine to provide them with the tools to transform a scientific or clinical question into research projects, and then pursue the answer to their question with the appropriate methods. The same skills also enable them to appraise the published literature in a systematic and rigorous manner. 

Each topic in the series began with a presentation and discussion of statistical principles and methods, then moved to a practical module using the principles to appraise a specific publication. Participants in the course had an immediate opportunity to try the techniques, both to demonstrate understanding and to reinforce the concepts to each learner. The articles of this series follow the same outline, providing clinicians of all specialties the basic statistical tools to conduct and appraise clinical research, along with a sample article for practicing each statistical method presented.

This Cleveland Clinic Journal of Medicine supplement includes 3 lectures from the “Biostatistics and Epidemiology Lecture Series.” Dr. Stoller’s presentation, The Architecture of Clinical Research, describes the basic structure of clinical research and the nomenclature to understand trial design and sources of bias.

Building on those concepts, Dr. Chatburn’s lecture, Basics of Study Design: Practical Considerations, outlines the structured approach to develop a formal research protocol. How to identify a problem, expand the scope of it through a literature review, create a hypothesis, design a study, and an introduction to basic statistical methods are discussed.

And in Chi-square and Fisher’s Exact Tests, Dr. Nowacki introduces the statistical methodology of these 2 tests to assess associations between 2 independent categorical variables. The sample article illustrates step-by-step calculation of both the large sample approximation (chi-square) and exact (Fisher’s) methodologies providing insight into how these tests are conducted.

My hope is that these articles, and future installments based on forthcoming lectures, are helpful to physicians both in conducting their own research and in evaluating the research of others

I am flattered to present the inaugural talk in the biostatistics and clinical research design series on the architecture of clinical research. This content is based on the teachings of my mentor, Dr. Alvan Feinstein, who together with Dr. David Sackett, is credited with pioneering clinical epidemiology. Dr. Feinstein was a Sterling Professor at the Yale School of Medicine. His main opus of work is a book called, Clinical Epidemiology: The Architecture of Clinical Research.¹ This paper is named in credit to Dr. Feinstein’s enormous contribution. I will review some important terms defined by Dr. Feinstein to provide the background necessary for the remainder of the talks in this series.

To start, I will frame this topic by asking the following question: Why do we do research? I’ll talk about the basic structure of research studies and provide a taxonomy, as Dr. Feinstein would say, a nomenclature with which to understand trial design and the sources of bias in those trials. Then, I will discuss these sources of bias in detail using the taxonomy that Dr. Feinstein described in his aforementioned book. Finally, I will share with you some examples of bias in clinical trials to help you better understand these concepts.

Now, the answer to the basic question posed above is: basically, we do cause-and-effect research to establish the causality of a risk factor or the efficacy of a therapy. Does cigarette smoking cause lung cancer? Does taking hydrochlorothiazide help systemic hypertension? Does air pollution worsen asthma? Does supplemental oxygen help patients with chronic obstructive pulmonary disease (COPD)?

Cause-and-effect research can be subsumed under 2 broad issues: causal risk factors and therapeutic efficacy. In his review of early false understandings in medicine that were based on anecdotal observation alone, Thomas cites many examples—“the undue longevity of useless and even harmful drugs can be laid at the door of authority,” ie, empiricism, lack of rigorous research.² The field is full of these: yellow fever causality, the value of cupping, and even intermittent mandatory ventilation when it was described by John Downs in 1973 and touted as a superior mode for weaning patients from mechanical ventilation.³ Twenty-five years later, randomized controlled trials by Brochard et al⁴ indicated not only that intermittent mandatory ventilation was not the best mode to wean but was, in fact, the worst mode for weaning patients from mechanical ventilation compared with either pressure support or spontaneous breathing trials. Many more examples exist to demonstrate the false understandings that can be ascribed to lack of rigorous study or evidence in medicine.

Before systematically exploring the sources of bias in Feinstein’s construct, let us define some very basic terms from his book. Dr. Feinstein talks about the baseline state, which refers to the group of patients under study who are culled from a larger population to whom the results are intended to be applied (Figure 1).¹ This baseline group is hopefully representative of this larger target population. As a nod to the later discussion, Dr. Feinstein would call bias introduced by unusual assembly of the study population from the larger intended population as “assembly bias.” So, if the group under study is not representative of either the patients you see or the world of patients with this condition or if there is something special or distinctively nonrepresentative about the study population, then the results may be subject to “assembly bias.” Assembly bias can compromise the so-called “external” validity of the study—its ability to be applied to populations beyond the study group.

Having assembled a baseline group for study, that group is classically allocated to 1 of 2 (or sometimes more than 2) compared therapies. In a controlled trial, patients can be allocated using a variety of strategies, including randomization. Using the paradigm diagram (Figure 1, which considers a 2-arm trial), patients are allocated to 1 of 2 compared groups—group A and group B. Then, in a treatment trial, 1 group receives the principal maneuver, which is the drug or intervention under study—for example, supplemental oxygen for patients with COPD. The comparative maneuver is allocated to group B, which also receives all the other treatments (called “co-maneuvers”) that are used to treat the condition under study. In a trial of supplemental oxygen for COPD evaluating lung function and exacerbation frequency as outcome measures, such co-maneuvers might include inhaled bronchodilators, inhaled corticosteroids, pulmonary rehabilitation, and Pneumovax vaccine. Ideally, these co-maneuvers are equally distributed between the compared groups (A and B).

So, in summary, we have a comparative maneuver, which is the nonadministration of supplemental oxygen in this proposed trial of supplemental oxygen in COPD, the principal maneuver—administration of oxygen—and all the co-maneuvers that are ideally equally distributed between both groups. This balanced distribution of co-maneuvers between the compared groups helps to ensure that any differences in the study outcome measures (ie, what is counted as the main impact of the intervention under study) can be solely attributed to the principal maneuver. When this condition—that the difference in outcomes can be reliably ascribed to the study intervention—is satisfied, the study is felt to be “internally” valid. As we will see, ensuring internal validity requires freedom from the many sources of what Dr. Feinstein calls “internal bias.”

Back to basic terms: “cohort” in Dr. Feinstein’s language is a group that shares common traits and is followed forward in a longitudinal study. The “outcome measure” is self-evident—it is what is being measured, with the “primary outcome” being the pre-defined measure that is considered the most important (and ideally most clinically relevant) impact of the study intervention. Later in this series of lectures, there will be discussions of power calculations and the so-called “effect size”—the magnitude of effect that the intervention is expected to produce and that is ideally deemed clinically important.

An important consideration in designing a trial is to define and declare the primary outcome measure carefully because defining the primary outcome measure has important implications for the study. I will provide an example from the alpha-1 antitrypsin deficiency literature. Some of you have probably read what has been called the RAPID trial.⁵ RAPID was a trial of augmentation therapy vs placebo in patients with severe alpha-1 antitrypsin deficiency. The primary outcome measure (which was pre-negotiated with the US Food and Drug Administration [FDA]) was computer tomography (CT) lung density determined at functional residual capacity (FRC) and total lung capacity (TLC). The trial failed to achieve statistical significance in regard to CT lung density, although the study authors argued that CT density measurements made at TLC were more reproducible than those made at FRC. When the results were analyzed by TLC alone, the results were statistically significant, but when they were analyzed with FRC and TLC combined, they were not. In the end, based on the pre-negotiated primary outcome measure of CT density based on both FRC and TLC, the FDA rejected the proposal for a label change to say that augmentation therapy slowed the loss of lung density even though the weight of evidence was clearly in its favor. This case exemplifies just how critical the choice of primary outcome measure can be.

The wash-out period refers to an interval in a subset of randomized trials called “crossover trials” in which the primary intervention is discontinued and the patient returns to his baseline state before the comparative maneuver is then implemented (Figure 2).⁶ In order to perform a crossover trial, it is important that the effects of the initial intervention can “wash out” or be fully extinguished. So, for example, in trials of radiation therapy vs surgery, it is impossible to do a crossover trial because the effects of radiation can never completely wash out nor can those of surgery, which are similarly permanent. For example, we cannot replace the colon once it is resected for cancer or replace the appendix once removed. Therefore, producing a wash-out requires some very specific pharmacokinetic and pharmacodynamic features in order for a crossover trial to be considered. Later talks in this series will discuss the enhanced statistical power of a crossover trial, where one is comparing every patient to him or herself rather than to another patient.

So, there is always an appetite to do a crossover trial as long as the criteria for wash-out can be met, namely again that the primary intervention can dissipate completely to the baseline state before the alternative intervention is implemented.

“Placebo” is a fairly self-evident and well-understood term; placebo refers to the administration of a maneuver in a way that is identical to the principal maneuver except that the placebo is not expected to exert any clinical effect.

“Blinding” is the unawareness of either the investigator or of the patient to which the intervention is being administered. “Single-blinding” refers to the condition in which either the study or the investigator (but not both) is unaware, and “double-blinding” refers to the condition in which both the subjects and the investigators are unaware. There can be some subtle issues that compromise whether the patient is aware of the intervention that he or she is receiving and that can potentially condition the patient’s response, particularly if there is any subjective component of the assessment of the outcome. So, blinding is important.

With these terms describing the elements of a clinical study now described, let us turn to the types of studies that comprise clinical research. The first group of study types is what Dr. Feinstein called descriptive studies—studies that simply describe phenomena without comparison to a control group. As an example of a descriptive study, Sehgal et al⁷ recently described the workup of a focal, segmental pneumonia in a patient taking pembrolizumab for lung cancer. In this paper, there were four other cases of focal pneumonia accompanying pembrolizumab use that were assembled from the literature, making this descriptive paper a so-called case series. A “case series” differs from a “single case report,” which reports a single patient experience. Though limited in their ability to establish cause and effect, case reports and case series can help researchers develop proof of principle, so I would not discount the value of case reports.⁸

I can cite a case report from of my own experience that demonstrates this point. In 1987, I saw a patient from Buffalo who had primary biliary cirrhosis and the hepatopulmonary syndrome (HPS). She was so debilitated by her HPS that she could not stand up without desaturating severely. Although she had normal liver synthetic function, she was severely debilitated by her HPS and the decision was made to offer her a liver transplant, which, at that time, was considered to be relatively contraindicated. Much to everyone’s amazement and satisfaction, her HPS completely resolved after the transplant surgery. Her oxygenation and alveolar-arterial oxygen gradient normalized, and her clubbing resolved. We reported this in a case report, which began to affect the way people thought about the feasibility of liver transplant for the HPS.⁸ The lesson is: do not underestimate the power of a thoughtful case report.

The second group of research study types is called “cohort studies,” in which one actually compares outcomes between 2 groups in the study. Cohort studies fall into the bucket of either “observational cohort studies,” in which allocation to the compared maneuvers is not performed by randomization but by any other strategy, and “randomized trials.” In observational studies, allocation could occur through physician choice, as when the physician prescribes a treatment to 1 group but not another, or by patient choice or circumstance. For example, an observational cohort study of the risk of cigarette smoking would compare outcomes between smokers and non-smokers where the patient choses to smoke under his/her own volition. Alternatively, the circumstances of an exposure could allocate someone to the principal maneuver, as when we are studying the effect of exposure to World Trade Center dust in the firefighters who responded or of exposure to nuclear radiation in Hiroshima survivors. These are examples of observational cohort studies that compare exposed individuals to unexposed individuals, where the exposure did not occur by randomization but by choice or unfortunate circumstance.

In contrast to observational studies, allocation in randomized trials occurs through a formal process. Randomization has the specific purpose of attempting to ensure that patients are allocated to 2 comparative groups from the baseline group with comparable risk for developing the outcome measure. When randomization is effective, differences in study outcomes can be reliably ascribed to the intervention rather than to differences in the baseline susceptibility of the compared groups.

While randomization is an excellent strategy to ensure baseline similarity between compared groups, randomization can fail, and its effectiveness must be checked. Specifically, in a randomized trial, it is customary to examine the compared groups at baseline on all features that can affect the likelihood of developing the outcome measure. If the groups turn out to be dissimilar at baseline in an important way, then the study is at risk for bias, which is specifically called “susceptibility bias” in Feinstein’s construct. Obviously, the larger number of baseline clinical and demographic features that can condition the likelihood of developing the outcome measure, the more difficult it is to achieve baseline similarity between compared groups and the more important it becomes to ensure that randomization has been effective. In this circumstance, larger numbers of participants in both compared groups are generally needed. More about susceptibility bias later.

There are generally 2 types of randomized trials: the so-called “parallel controlled trials” in which each group receives either the principal or the comparative maneuver and is followed and “crossover trials” in which each compared group receives both the principal maneuver and the co-maneuver at different times after an effective wash-out period. Wash-out was discussed above. Figure 2 shows an example of a crossover trial examining the effects of terbutaline on diaphragmatic function.⁶ The investigators administered terbutaline for a week, measured transdiaphragmatic pressures, gave the patient a terbutaline vacation (the “wash-out period”), and then crossed over those patients who were initially receiving terbutaline to placebo and initial placebo recipients to terbutaline, having remeasured diaphragmatic function after the wash-out period to assure that the patient’s diaphragmatic function prior to the second crossover was identical to his/her baseline state. If this return to baseline is accomplished, then the criteria from effective wash-out are satisfied.

As we begin to talk about sources of bias, consider a study in which we compare survival of patients allocated to surgery vs nonsurgical therapy for lung cancer (Figure 3).¹ This study is subject to the first type of so-called “internal bias” in the Feinsteinian construct—so-called “selection bias.” For example, all patients treated surgically were considered healthy enough by their doctors to undergo surgery, whereas patients treated without surgery may have been deemed inoperable because of comorbidities, lung dysfunction, cardiac dysfunction, and so on. If the results of such a comparison show that the mortality rate among surgical patients in this study was lower, the question then becomes: is the improved survival in surgical candidates due to the superior efficacy of surgery vs other therapy or was the enhanced survival due to the surgical patients being healthier to begin with? You can intuitively sense that the answer to this question is that the enhanced survival may be due to the better health of patients treated surgically rather than to the surgery itself because of how the patients were selected to receive it. So, this is a simple example of what Dr. Feinstein would call “susceptibility bias.” Susceptibility bias occurs when the 2 baseline groups are not comparably at risk or susceptible to developing the outcome measure, leading the naïve investigator in this specific example to attribute the difference in outcomes to the superiority of surgery when in fact it may have nothing to do with the surgery vs. the other maneuver. When susceptibility bias is in play, the difference between the outcomes in the compared groups could be attributed to the baseline imbalance of the groups rather than to the principal maneuver itself.

Turning back to the taxonomy of bias, there are four types that can threaten internal validity—“susceptibility,” “performance,” “detection,” and “transfer” bias—and 1 type of bias (called “external bias”) that can affect the generalizability of the study called “assembly bias” (Table 1).

Figure 4 shows where these various sources of bias appear in the architecture of a clinical trial. As just discussed, susceptibility bias affects the baseline state and the comparability of the groups. Performance bias relates to how effective and how comparably the co-maneuvers are given and whether the primary intervention is potent enough to affect an outcome. Both transfer and detection bias operate in detecting the outcome, especially regarding the rigor and frequency with which they are investigated. Transfer bias has to do with selective loss to follow-up of those included in the trial. If there is a systematic reason for loss to follow-up that is related to the impact of the intervention, then the study is at risk for transfer bias. For example, in a randomized trial of drug A vs placebo for pneumonia, if drug A is effective but all the drug A recipients fail to follow-up because they feel too good to return for follow-up, then transfer bias could be causing the study to show nonefficacy even though the drug works. So, if those who respond favorably are systematically lost to follow-up, and if all the patients who felt lousy wanted to see the doctor and came back for follow-up, such transfer bias would bias towards nonefficacy. Specifically, only patients remaining in the trial would be those who failed to respond and that would dilute any difference between the 2 groups despite the active efficacy of drug A.

Hopefully, you are already beginning to get a sense that one has to be extremely disciplined in thinking about each of these sources of bias because they can have some very subtle nuances in randomized trials that can easily escape attention.

Returning to sources of bias, let’s consider the second type of bias, “performance bias.” Performance bias relates to the administration of the compared maneuvers—the primary or principal maneuver, compared with the comparative maneuver. Performance bias can occur when the main maneuver is not administered adequately or when the co-maneuvers are administered in an imbalanced way between the compared groups. Consider the example of the Long-Term Oxygen Treatment Trial (LOTT) trial, which compared use of supplemental oxygen with no supplemental oxygen in patients with stable COPD and resting or exercise-induced moderate desaturation.⁹ The principal outcome measure of LOTT was all-cause hospitalization or death. In such a study, many potential sources of performance bias exist. For example, performance bias might exist if none of the patients allocated to oxygen actually used supplemental oxygen. Alternately, to the extent that use of inhaled corticosteroids or antimuscarinic agents lessens the risk of COPD exacerbation, performance bias could occur if use of these co-maneuvers was imbalanced between the compared groups. As a specific extreme circumstance, if all patients in the nonoxygen group used these inhalers but none of the patients in the oxygen group did, then a lack of difference between exacerbation frequency could be related to this imbalance in co-maneuvers (a form of performance bias) rather than to the lack of efficacy of supplemental oxygen.

“Compliance bias” is a subset of performance bias which occurs when 2 conditions are satisfied: (1) the main maneuver is not administered adequately, and (2) the investigator is unaware of that nonreceipt so that this cannot be accounted for in interpreting the study results. For example, if a drug has efficacy but if no one in the treatment arm of the trial takes the drug, the absence of a difference in outcomes between the compared groups will be ascribed to nonefficacy, whereas “compliance bias” (ie, no one actually took the drug) could actually be the cause. Ideally, randomized studies should be evaluated on an “intention to treat” basis irrespective of compliance, but there is an analytic approach called “per protocol” analysis in which you can analyze the results according to whether the patient actually used the intervention in an effective way. “Per protocol” analysis is a secondary analysis of the primary results but it can nonetheless help determine whether the negative result is likely related to noncompliance or not.

A third type of internal bias, “detection bias,” is fairly straightforward. Detection bias is related to how avidly and how comparably the outcomes are measured between the 2 compared groups. Let’s say that you are conducting a trial of a new antibiotic and the primary outcome is colony counts on petri dishes of plated collected specimens. If the technicians who read the petri dish counts are unblinded, they may look at the colony counts with a biased eye, seeing fewer colonies on plates collected from patients receiving the antibiotic.

Overall, detection bias occurs when outcomes are ascertained or detected unequally between the compared groups, and detection bias can involve any of the following: is there comparable surveillance of the 2 groups for analysis of the outcome measure? Are the diagnostic tests comparably performed in both groups and is the interpretation comparably unbiased with equipoise? Investigators who know which patients are receiving an active drug and those who are not could experience subliminal bias that renders them more likely to find that the drug under study is efficacious.

Depending on the principal study maneuver, ensuring blinding can be challenging. To demonstrate this point, let’s consider the example of conducting a randomized control trial of Vicks VapoRub. Vicks VapoRub is an old product that smells like wintergreen and that mothers used to rub on the chests of their infants in the hope of speeding recovery from colds and bronchitis episodes. It was felt that the distinctive smell of the product was materially related to wintergreen, which gives rise to the odor. So, imagine a randomized trial of Vicks VaporRub. A trial is designed in which sick children receive Vicks VapoRub on their chest and others receive a placebo rub that lacks the distinctive wintergreen odor. But, the odor itself is felt to be related to how Vicks VapoRub actually works. Thus, it is the odor itself that creates the blinding challenge here.

The primary outcomes in this study are the duration of the child’s cold symptoms, as ascertained by pediatricians actually examining the children. So, pediatricians would come and listen to the infants’ chests: “Yeah, this chest is clear, but this other infant is still full of rhonchi,” and they would ascertain the outcome measure in this way. So, my blinding question to you is: how do you blind a trial of Vicks VapoRub given the conditions described? Namely, you put the VapoRub on the chest, it smells and the smell is the intervention—how do you blind such a trial? 

The clever answer is that you should put Vicks VapoRub on the upper lips of all the examiners, so what they smell is Vicks VapoRub independent of whether the child they are examining also has the Vicks VapoRub or placebo on their chest. In this way, single blinding of the examiners is preserved and detection bias is averted. It is important to point out that double blinding could also be achieved by placing Vicks VapoRub on the child’s upper lip, but there is little reason to suspect that the infants being studied have a bias related to whether they smell the Vicks VapoRub.

The fourth potential source of internal bias is called “transfer bias.” Transfer bias is the selective loss to follow-up of patients from 1 of the 2 compared groups in the trial for a systematic reason. By systematic, I mean that that the drop-out is associated with the development of the outcome event or some impact of the intervention regarding the likelihood to develop the outcome event. As an example, if all patients respond favorably to a drug and everybody fails to follow up because they feel too good to come back, then that would bias the study towards nonefficacy even in the face of an efficacious intervention.

Finally, let’s consider a source of bias that can affect the “external validity,” or the generalizability of the study results to populations other than that included in the study itself. Dr. Feinstein calls this 5th type of bias “assembly bias” (Table 1).¹ Assembly bias occurs when the results of the study cannot be reliably applied to populations outside the study itself.

For example, if I screen patients during a study of digoxin for heart rate control in atrial fibrillation, I could establish whether the subject was compliant or not by checking his/her serum digoxin levels. Serum levels of 0 indicate that the patient has not taken the digoxin. If I include a run-in period for the trial—an interval before the actual study when I am assessing potential subjects’ eligibility to participate—and check serum digoxin levels to include only patients who are shown to be taking the drug, then I am screening for study inclusion on compliance. In this way, I will have assembled a population that is highly compliant so that I can truly assess whether digoxin has efficacy in controlling the heart rate in patients with atrial fibrillation. At the same time, this study population is not highly representative of the population of patients with atrial fibrillation at large, because we know that rates of drug noncompliances may be as high as 30% to 40%. So, culling a population with run-in periods on demonstrated compliance criteria may be very important to assess efficacy (ie, whether the drug works), but this design will trade off on the effectiveness of the drug (ie, which asks the question “does the drug work in actual practice?”). This is because, in the yin-yang between assessing efficacy and assessing effectiveness, the focus on assessing efficacy naturally undermines the ability to assess whether the drug works in real-world conditions.

As another example of potential assembly bias, let’s say you are studying an antihypertensive drug at a Veterans Administration (VA) hospital, where most veterans are men. But you are treating women in your practice and wonder whether the drug, which works in a predominately male population, will work in your female patients. So, there could be assembly bias in applying the results of a VA study to a non-VA predominantly female population.

Having now described the design of clinical trials and the major sources of bias, let’s apply this thinking to the earliest clinical trial. James Lind, a British Naval officer, was credited with conducting the first clinical trial of citrus fruits for scurvy while sailing on the ship Salisbury in 1747.² The question that Lind addressed was “does citrus fruit treat and prevent scurvy?” In describing this trial, Lind stated “I took 12 patients with scurvy, these patients were as similar as I could have them, had one diet common to all.” As you read this through your new Feinsteinian bias lens, Lind is addressing 2 potential sources of bias, namely, susceptibility bias and performance bias. In trying to make the “cases as similar as I could have them,” he is trying to avoid susceptibility bias and in “providing one diet common to all,” he is trying to avoid performance bias.

In terms of the intervention in this trial, these 12 patients were allocated in pairs to several interventions: a quart of cider a day, 25 drops of elixir of vitriol 3 times a day on an empty stomach, 2 spoonsful of vinegar 3 times a day on an empty stomach, ½ pint a day of sea water, 2 oranges and 1 lemon given every day, and a “bigness of nutmeg” 3 times per day. In describing the outcome of the trial, Lind states “the consequence was that the most sudden and visible good effects were perceived from the use of oranges and lemons; one of those who had taken them, being at the end of 6 days fit for duty. The spots were not indeed at that time quite off his body, nor his gums sound, but without any other medicine then a gargarism of elixir vitriol, he became quite healthy before we came into Plymouth which was on the 16th of June. The other was the best recovered of any in his condition; and being now deemed pretty well, was appointed nurse to the rest of the sick.”

In analyzing this trial, we could characterize it as a parallel controlled trial. Whether the allocation was done by randomization is not clear, but it was certainly an observational cohort study in that there were concurrent controls who were treated as similarly as possible except for the principal maneuver, which was the administration of citrus fruit. Already mentioned was the attention to averting susceptibility and performance bias. There was no evidence of compliance bias as the interventions were enforced, nor was there evidence of transfer bias because all subjects who were enrolled in the study completed the study because they were a captive group on a sailing ship. Finally, the likelihood of assembly bias seems small, as these sailors seemed to be representative of victims of scurvy in general, namely in being otherwise deprived of access to citrus fruits.

In terms of the statistical results of this study, subsequent analysis of the research showed that the impact of lemons and oranges was dramatic and showed a trend (P = .09) towards statistical significance. Notwithstanding the lack of a P < .05, Dr. Feinstein would likely say that this study satisfied the “intra-ocular test” in that the efficacy of the citrus fruit was so dramatic that it “hit you between the eyes.” He often argued that the widespread practice of prescribing penicillin for pneumococcal pneumonia was not based on the results of a convincing randomized controlled trial because the efficacy of penicillin in that setting was so dramatic that a randomized trial was not necessary (and potentially even unethical if the condition of “intra-ocular” efficacy was satisfied).

The final question to address in this lecture is whether randomized controlled trials, for all their rigor, always produce more reliable results than observational studies. This issue has been addressed by several authors.^10–12 Sacks et al¹⁰ contended in 1983 that observational studies systematically overestimate the magnitude of association between exposure and outcome and therefore argued that randomized trials were more reliable than observational studies. Subsequent analyses tended to challenge this view.^11,12 Specifically, Benson and Hartz¹¹ compared the results of 136 reports regarding 19 different therapies that were studied between 1985 and 1998. In only 2 of the 19 analyses did the treatment effects in the observational studies fall outside the 95% confidence interval for the randomized controlled trial results. In this way, these authors argued that observational studies generally are concordant with the results of randomized trials. They stated that “our finding that observational studies and randomized controlled trials usually produce similar results differs from the conclusions of previous authors. The fundamental criticism of observational studies is that unrecognized confounding factors may distort the results. According to the conventional wisdom, this distortion is sufficiently common and unpredictable that observational studies are not liable and should not be funded. Our results suggested observational studies usually do provide valid information.”¹¹

An additional analysis of this issue was performed by Concato et al,¹² who identified 99 articles regarding 5 clinical topics. Again, the results from randomized trials were compared with those of observational cohort or case-controlled studies regarding the same intervention. The authors reported that “contrary to prevailing belief, the average results from well-designed observational studies did not systematically overestimate the magnitude of the associations between exposure and outcome as compared with the results of randomized, controlled trials on the same topic. Rather, the summary results of randomized, controlled trials and observational studies were remarkably similar.”¹²

On the basis of these studies, it appears that randomized control trials continue to serve as the gold standard in clinical research, but we must also recognize that circumstances often preclude the conduct of a randomized trial. As an example, consider a randomized trial of whether cigarette smoking is harmful, which, given the strong suspicion of harm, would be unethical in that patients cannot be randomized to smoke. Similarly, from the example before, a randomized trial of penicillin for pneumococcal pneumonia would be unethical because denying patients in the placebo group access to penicillin would exclude them from access to a drug that has “intra-ocular” efficacy. In circumstances like these, well-performed observational studies that are attentive to sources of bias can likely produce comparably reliable results to randomized trials.

In the end, of course, the interpretation of the study results requires the reader’s careful attention to potential sources of bias that can compromise study validity. The hope is that with Dr. Feinstein’s framework, you can be better equipped to think critically about study results that you review and to keenly ascertain whether there is any threat to internal or to external validity. Similarly, as you go on to design clinical trials yourselves, you can pay attention to these potential sources of bias that, if present, can compromise the reliability of the study conclusions internally or their applicability to patients outside of the study.

I am flattered to present the inaugural talk in the biostatistics and clinical research design series on the architecture of clinical research. This content is based on the teachings of my mentor, Dr. Alvan Feinstein, who together with Dr. David Sackett, is credited with pioneering clinical epidemiology. Dr. Feinstein was a Sterling Professor at the Yale School of Medicine. His main opus of work is a book called, Clinical Epidemiology: The Architecture of Clinical Research.¹ This paper is named in credit to Dr. Feinstein’s enormous contribution. I will review some important terms defined by Dr. Feinstein to provide the background necessary for the remainder of the talks in this series.

To start, I will frame this topic by asking the following question: Why do we do research? I’ll talk about the basic structure of research studies and provide a taxonomy, as Dr. Feinstein would say, a nomenclature with which to understand trial design and the sources of bias in those trials. Then, I will discuss these sources of bias in detail using the taxonomy that Dr. Feinstein described in his aforementioned book. Finally, I will share with you some examples of bias in clinical trials to help you better understand these concepts.

Now, the answer to the basic question posed above is: basically, we do cause-and-effect research to establish the causality of a risk factor or the efficacy of a therapy. Does cigarette smoking cause lung cancer? Does taking hydrochlorothiazide help systemic hypertension? Does air pollution worsen asthma? Does supplemental oxygen help patients with chronic obstructive pulmonary disease (COPD)?

Cause-and-effect research can be subsumed under 2 broad issues: causal risk factors and therapeutic efficacy. In his review of early false understandings in medicine that were based on anecdotal observation alone, Thomas cites many examples—“the undue longevity of useless and even harmful drugs can be laid at the door of authority,” ie, empiricism, lack of rigorous research.² The field is full of these: yellow fever causality, the value of cupping, and even intermittent mandatory ventilation when it was described by John Downs in 1973 and touted as a superior mode for weaning patients from mechanical ventilation.³ Twenty-five years later, randomized controlled trials by Brochard et al⁴ indicated not only that intermittent mandatory ventilation was not the best mode to wean but was, in fact, the worst mode for weaning patients from mechanical ventilation compared with either pressure support or spontaneous breathing trials. Many more examples exist to demonstrate the false understandings that can be ascribed to lack of rigorous study or evidence in medicine.

Before systematically exploring the sources of bias in Feinstein’s construct, let us define some very basic terms from his book. Dr. Feinstein talks about the baseline state, which refers to the group of patients under study who are culled from a larger population to whom the results are intended to be applied (Figure 1).¹ This baseline group is hopefully representative of this larger target population. As a nod to the later discussion, Dr. Feinstein would call bias introduced by unusual assembly of the study population from the larger intended population as “assembly bias.” So, if the group under study is not representative of either the patients you see or the world of patients with this condition or if there is something special or distinctively nonrepresentative about the study population, then the results may be subject to “assembly bias.” Assembly bias can compromise the so-called “external” validity of the study—its ability to be applied to populations beyond the study group.

Having assembled a baseline group for study, that group is classically allocated to 1 of 2 (or sometimes more than 2) compared therapies. In a controlled trial, patients can be allocated using a variety of strategies, including randomization. Using the paradigm diagram (Figure 1, which considers a 2-arm trial), patients are allocated to 1 of 2 compared groups—group A and group B. Then, in a treatment trial, 1 group receives the principal maneuver, which is the drug or intervention under study—for example, supplemental oxygen for patients with COPD. The comparative maneuver is allocated to group B, which also receives all the other treatments (called “co-maneuvers”) that are used to treat the condition under study. In a trial of supplemental oxygen for COPD evaluating lung function and exacerbation frequency as outcome measures, such co-maneuvers might include inhaled bronchodilators, inhaled corticosteroids, pulmonary rehabilitation, and Pneumovax vaccine. Ideally, these co-maneuvers are equally distributed between the compared groups (A and B).

So, in summary, we have a comparative maneuver, which is the nonadministration of supplemental oxygen in this proposed trial of supplemental oxygen in COPD, the principal maneuver—administration of oxygen—and all the co-maneuvers that are ideally equally distributed between both groups. This balanced distribution of co-maneuvers between the compared groups helps to ensure that any differences in the study outcome measures (ie, what is counted as the main impact of the intervention under study) can be solely attributed to the principal maneuver. When this condition—that the difference in outcomes can be reliably ascribed to the study intervention—is satisfied, the study is felt to be “internally” valid. As we will see, ensuring internal validity requires freedom from the many sources of what Dr. Feinstein calls “internal bias.”

Back to basic terms: “cohort” in Dr. Feinstein’s language is a group that shares common traits and is followed forward in a longitudinal study. The “outcome measure” is self-evident—it is what is being measured, with the “primary outcome” being the pre-defined measure that is considered the most important (and ideally most clinically relevant) impact of the study intervention. Later in this series of lectures, there will be discussions of power calculations and the so-called “effect size”—the magnitude of effect that the intervention is expected to produce and that is ideally deemed clinically important.

An important consideration in designing a trial is to define and declare the primary outcome measure carefully because defining the primary outcome measure has important implications for the study. I will provide an example from the alpha-1 antitrypsin deficiency literature. Some of you have probably read what has been called the RAPID trial.⁵ RAPID was a trial of augmentation therapy vs placebo in patients with severe alpha-1 antitrypsin deficiency. The primary outcome measure (which was pre-negotiated with the US Food and Drug Administration [FDA]) was computer tomography (CT) lung density determined at functional residual capacity (FRC) and total lung capacity (TLC). The trial failed to achieve statistical significance in regard to CT lung density, although the study authors argued that CT density measurements made at TLC were more reproducible than those made at FRC. When the results were analyzed by TLC alone, the results were statistically significant, but when they were analyzed with FRC and TLC combined, they were not. In the end, based on the pre-negotiated primary outcome measure of CT density based on both FRC and TLC, the FDA rejected the proposal for a label change to say that augmentation therapy slowed the loss of lung density even though the weight of evidence was clearly in its favor. This case exemplifies just how critical the choice of primary outcome measure can be.

The wash-out period refers to an interval in a subset of randomized trials called “crossover trials” in which the primary intervention is discontinued and the patient returns to his baseline state before the comparative maneuver is then implemented (Figure 2).⁶ In order to perform a crossover trial, it is important that the effects of the initial intervention can “wash out” or be fully extinguished. So, for example, in trials of radiation therapy vs surgery, it is impossible to do a crossover trial because the effects of radiation can never completely wash out nor can those of surgery, which are similarly permanent. For example, we cannot replace the colon once it is resected for cancer or replace the appendix once removed. Therefore, producing a wash-out requires some very specific pharmacokinetic and pharmacodynamic features in order for a crossover trial to be considered. Later talks in this series will discuss the enhanced statistical power of a crossover trial, where one is comparing every patient to him or herself rather than to another patient.

So, there is always an appetite to do a crossover trial as long as the criteria for wash-out can be met, namely again that the primary intervention can dissipate completely to the baseline state before the alternative intervention is implemented.

“Placebo” is a fairly self-evident and well-understood term; placebo refers to the administration of a maneuver in a way that is identical to the principal maneuver except that the placebo is not expected to exert any clinical effect.

“Blinding” is the unawareness of either the investigator or of the patient to which the intervention is being administered. “Single-blinding” refers to the condition in which either the study or the investigator (but not both) is unaware, and “double-blinding” refers to the condition in which both the subjects and the investigators are unaware. There can be some subtle issues that compromise whether the patient is aware of the intervention that he or she is receiving and that can potentially condition the patient’s response, particularly if there is any subjective component of the assessment of the outcome. So, blinding is important.

With these terms describing the elements of a clinical study now described, let us turn to the types of studies that comprise clinical research. The first group of study types is what Dr. Feinstein called descriptive studies—studies that simply describe phenomena without comparison to a control group. As an example of a descriptive study, Sehgal et al⁷ recently described the workup of a focal, segmental pneumonia in a patient taking pembrolizumab for lung cancer. In this paper, there were four other cases of focal pneumonia accompanying pembrolizumab use that were assembled from the literature, making this descriptive paper a so-called case series. A “case series” differs from a “single case report,” which reports a single patient experience. Though limited in their ability to establish cause and effect, case reports and case series can help researchers develop proof of principle, so I would not discount the value of case reports.⁸

I can cite a case report from of my own experience that demonstrates this point. In 1987, I saw a patient from Buffalo who had primary biliary cirrhosis and the hepatopulmonary syndrome (HPS). She was so debilitated by her HPS that she could not stand up without desaturating severely. Although she had normal liver synthetic function, she was severely debilitated by her HPS and the decision was made to offer her a liver transplant, which, at that time, was considered to be relatively contraindicated. Much to everyone’s amazement and satisfaction, her HPS completely resolved after the transplant surgery. Her oxygenation and alveolar-arterial oxygen gradient normalized, and her clubbing resolved. We reported this in a case report, which began to affect the way people thought about the feasibility of liver transplant for the HPS.⁸ The lesson is: do not underestimate the power of a thoughtful case report.

The second group of research study types is called “cohort studies,” in which one actually compares outcomes between 2 groups in the study. Cohort studies fall into the bucket of either “observational cohort studies,” in which allocation to the compared maneuvers is not performed by randomization but by any other strategy, and “randomized trials.” In observational studies, allocation could occur through physician choice, as when the physician prescribes a treatment to 1 group but not another, or by patient choice or circumstance. For example, an observational cohort study of the risk of cigarette smoking would compare outcomes between smokers and non-smokers where the patient choses to smoke under his/her own volition. Alternatively, the circumstances of an exposure could allocate someone to the principal maneuver, as when we are studying the effect of exposure to World Trade Center dust in the firefighters who responded or of exposure to nuclear radiation in Hiroshima survivors. These are examples of observational cohort studies that compare exposed individuals to unexposed individuals, where the exposure did not occur by randomization but by choice or unfortunate circumstance.

In contrast to observational studies, allocation in randomized trials occurs through a formal process. Randomization has the specific purpose of attempting to ensure that patients are allocated to 2 comparative groups from the baseline group with comparable risk for developing the outcome measure. When randomization is effective, differences in study outcomes can be reliably ascribed to the intervention rather than to differences in the baseline susceptibility of the compared groups.

While randomization is an excellent strategy to ensure baseline similarity between compared groups, randomization can fail, and its effectiveness must be checked. Specifically, in a randomized trial, it is customary to examine the compared groups at baseline on all features that can affect the likelihood of developing the outcome measure. If the groups turn out to be dissimilar at baseline in an important way, then the study is at risk for bias, which is specifically called “susceptibility bias” in Feinstein’s construct. Obviously, the larger number of baseline clinical and demographic features that can condition the likelihood of developing the outcome measure, the more difficult it is to achieve baseline similarity between compared groups and the more important it becomes to ensure that randomization has been effective. In this circumstance, larger numbers of participants in both compared groups are generally needed. More about susceptibility bias later.

There are generally 2 types of randomized trials: the so-called “parallel controlled trials” in which each group receives either the principal or the comparative maneuver and is followed and “crossover trials” in which each compared group receives both the principal maneuver and the co-maneuver at different times after an effective wash-out period. Wash-out was discussed above. Figure 2 shows an example of a crossover trial examining the effects of terbutaline on diaphragmatic function.⁶ The investigators administered terbutaline for a week, measured transdiaphragmatic pressures, gave the patient a terbutaline vacation (the “wash-out period”), and then crossed over those patients who were initially receiving terbutaline to placebo and initial placebo recipients to terbutaline, having remeasured diaphragmatic function after the wash-out period to assure that the patient’s diaphragmatic function prior to the second crossover was identical to his/her baseline state. If this return to baseline is accomplished, then the criteria from effective wash-out are satisfied.