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More Information on the Design of Clinical Trials

Issues in Clinical Trials of New Drugs for Community-Acquired Bacterial Pneumonia

December 9, 2009

James Floyd, M.D.
Health Researcher, Health Research Group at Public Citizen
FDA Anti-Infective Drugs Advisory Committee

View this testimony as a pdf 

The draft guidance under discussion clarifies several important issues regarding the appropriate design and conduct of noninferiority (NI) trials for community-acquired bacterial pneumonia (CABP). Overall, the recommendations in the guidance are a dramatic improvement over the current practice, and the FDA should be congratulated for their efforts. Because essentially all clinical trials of new antibiotics for CABP over the last two decades have been NI trials, I will limit my comments to this topic.


Everyone here agrees that new antibiotics, particularly those active against resistant pathogens, are desirable. However, new antibiotics are desirable only if they are effective. Approving new antibiotics that are less effective than current treatments under the guise of similar efficacy puts patients at risk. First, trials must be designed so that they have the capacity to demonstrate efficacy. Then, issues of feasibility can be considered.

  

An amendment to the federal Food, Drug, and Cosmetic Act in 1962 established "adequate and well-controlled studies" as the basis for determining the efficacy of new drugs, and this was codified in 1985. On active control studies, 21 CFR 314.126 states that "Similarity of test drug and active control can mean either that both drugs were effective or that neither was effective." The features of trial design and conduct that allow one to distinguish between these two scenarios are detailed by the International Conference on Harmonization (ICH) in documents E-9 and E-10, and my comments are derived from the scientific issues presented in these documents.

NI trials do not show that two treatments are equivalent to each other. Rather, they exclude that one treatment is worse than another by a prespecified, clinically acceptable margin. For a NI comparison to be valid: (1) evidence of a treatment effect of the active control must be reliable and reproducible, (2) the trial design must reflect the patient and disease characteristics, concomitant treatments, and outcomes of previous controlled trials, (3) the trial must be conducted in a way that minimizes bias towards similar treatment effect, and (4) the margin selected must be justified clinically.

The FDA has provided compelling evidence from historical data and previous controlled trials of a substantial treatment effect for antibiotics in CABP, and estimates of this effect are presented in the draft guidance. A few points about these data are worth mentioning. First, nearly all patients had pneumococcal or lobar pneumonia. There is little reliable and reproducible evidence for a treatment effect with atypical pathogens from which a noninferiority margin can be calculated. Second, the effect size was greatest in patients at highest risk of death, those with bacteremia and over age 50. Third, an arguably reliable estimate for a treatment effect exists for the endpoint of mortality, but not for intermediate clinical outcomes or surrogate endpoints.

Today, the FDA presented data from observational studies that strongly suggest a treatment effect for signs and symptoms of pneumonia, and these studies are similar in design to the studies of mortality. This was an impressive review of the evidence, and I have little doubt that effective antibiotics improve symptoms. Then why is mortality a reasonable endpoint for NI trials while signs and symptoms are not? Signs and symptoms are subjective and were poorly defined in these early studies, rendering them irreproducible. Even contemporary studies suggest that clinicians have difficulty corroborating physical findings. On the other hand, death is an objective outcome, the most objective outcome, and has not varied from 1940 to 2009.

Additionally, the Infectious Diseases Society of America position paper on the design of clinical trials in CABP refers to a placebo-controlled RCT of tetracycline in young men with mild CAP, 46% of whom had evidence of Mycoplasma pnuemoniae [1]. This trial showed that tetracycline improved biomarkers, such as temperature and infiltrate on CXR, as well as symptoms, such as cough and fatigue [2]. However, a valid endpoint cannot be constructed from these biomarkers and symptoms, and therefore an accurate estimate of effect size cannot be determined from this trial.

 

Effectiveness of Active Control

 

Bacteremic Subjects

Nonbacteremic subjects

Age Group, variable 

No specific treatment

Antibiotic treatment

No specific treatment

Antibiotic treatment

12-29 years

No. of deaths/no of patients (% mortality)

81/126 (64.29)

5/21 (23.81)

90/1036 (8.69)

4/97 (4.12)

% Difference (95% CI)

40 (20-61)

5 (0-9)

Proposed margin, %

10

None

30-49 years

No. of deaths/no of patients (% mortality)

319/428 (74.53)

23/81 (28.40)

218/1222 (17.84)

14/171 (8.19)

% Difference (95% CI)

46 (35-57)

10 (5-14)

Proposed margin, %

10

2.5

≥50 years

No. of deaths/no of patients (% mortality)

368/395 (93.16)

40/84 (47.62)

353/715 (49.37)

23/143 (16.08)

% Difference (95% CI)

46 (35-57)

33 (26-40)

Proposed margin, %

10

10

Fleming TR, Powers JH. CID. 2008;47:S108-200.

This table comes from a review of the evidence for a treatment effect of antibiotics in CABP by Fleming and Powers, with mortality stratified by age and bacteremia status[3]. The evidence for a treatment effect on mortality is much clearer in bacteremic patients and those over the age of 50, as is effect modification by these variables.

For one to assume constancy of effect in contemporary trials, patients who are at high risk of death must be enrolled. Also, the primary efficacy analysis must include only those patients with microbiologic evidence of typical bacterial pathogens, called the MITT population in the draft guidance. Failing to do so may result in similar outcomes between treatment groups in the study population, while in patients at higher risk of death and with typical pathogens the experimental treatment may be substantially worse than the active control. The draft guidance makes both of these points very clearly.

Patients who receive any prior antibacterial drug therapy should not be enrolled in NI trials, as this minimizes any difference in treatment effect between two drugs and can lead to a false NI inference. There is evidence to support this, and by default we should assume that this is the case. Concomitant antibacterial drug therapy should not be allowed for similar reasons. Any patients who do receive concomitant antibacterial drug therapy should not be excluded from analysis, because such post-randomization exclusions are likely to introduce bias. The current draft guidance also makes these points very clearly.

A recent example highlights the pitfalls of improperly designed and executed NI trials. In June 2009, this advisory committee evaluated two trials that compared cethromycin with clarithromycin for the outpatient treatment of mild to moderate CABP [4]. In these trials, half of patients had a PORT score of 1 and less than 1% died. Typical bacterial pathogens were recovered in less than a quarter of patients. Prior antibiotics were given in over 10% of the study population and nearly 15% of patients were excluded from one of two primary efficacy analyses based on post-randomization events, including the use of concomitant antibiotics.

When patients with a PORT score of 1, patients with atypical pathogens, and patients who received prior antibiotics were excluded, less than half the initial study population remained and cure rates were much lower. In one of the two studies, excluding these patients made the treatment difference larger, with cethromycin appearing worse than clarithromycin. In other words, diluting the sample with patients who were not sick and did not have typical pathogens and giving prior antibiotics may have obscured the inferiority of cethromycin. The deficiencies in these trials are not unique – they plague nearly all contemporary trials in CABP and bring into question the claims of efficacy of some previously approved treatments.

One flaw in the draft guidance is the designation of "clinical response" as an appropriate primary endpoint in NI trials. This is a composite outcome that includes mortality and the resolution of signs and symptoms. In doing so, the following assumptions are made: (1) mortality is one of several types of clinical failure, (2) any treatment effect on clinical failure will be larger than the effect on mortality, and (3) a treatment effect on mortality is unlikely to be observed in contemporary trials because of rescue therapies and supportive care, such as mechanical ventilation. Let us explore the second and third assumptions. 

First, there is no evidence that a treatment effect on biomarkers of disease and resolution of symptoms reliably predicts an effect on mortality. In fact, the opposite can be seen. In DORI-09, a multicenter phase 3 trial that compared doripenem to piperacillin/tazobactam in patients with ventilator association pneumonia, there was no difference in clinical response rates [5]. However, doripenem resulted in a significant increase in mortality during treatment.

 

Second, the myth that patients no longer die of pneumonia because of rescue therapies and advances in supportive care is not supported by evidence. 55,477 Americans died of pneumonia in 2006, according to the National Center for Health Statistics [6], and current mortality from CABP in hospitalized patients was estimated at 15% in a recent observational study [7]. The low mortality rate seen in contemporary trials of CABP reflects the sampling of patients who are at low risk of death. Furthermore, challenging the assumption of constancy of effect because of the much lower mortality rate observed in contemporary trials does not argue for changing the endpoint to an unvalidated surrogate measure. It argues against the use of NI trials to demonstrate efficacy and in favor conducting superiority trails.

The assumptions required to extrapolate from mortality to clinical response are not based on evidence, and they appear likely to be untrue. This is precisely the reason that any endpoint evaluated in a NI trial must be one for which there is reliable and reproducible evidence of a treatment effect for the active control.

 

To derive the NI margin, both statistical reasoning and clinical judgment must be used. M1, the lower bound of the confidence interval for the estimated treatment effect of antibiotics in CABP is estimated at 9-15% by the FDA. Clinical judgment must be used to determine how much loss of efficacy is acceptable in setting M2. Although M1 may be large, especially in subgroups at higher risk of death, a large M2 cannot be justified for a life-saving therapy. Most clinicians would find it difficult to justify using a treatment that results in a 10% increase in mortality over existing effective therapies.

Consistent with the presentation by the FDA today, an odds ratio based approach to NI margins may offer more flexibility in enrolling some patients who are not in the highest risk categories, while maintaining the validity of the margin selected. Nonetheless, study populations will be smaller if patients at higher risk are enrolled, creating a clear incentive for this favorable feature of trial design.
The issues raised today are not arbitrary or merely statistical side notes. NI trials that violate principles of good study design and conduct are unable to demonstrate the efficacy of new treatments. If a trial has no capacity to demonstrate efficacy, it no longer matters whether or not it is feasible. As a clinician, I am not interested in a new antibacterial therapy if I have to worry about whether or not it is less effective than existing treatments because of poor study design and conduct.

References

[1] Kingston JR, et al. JAMA. 1961;176:118-125.
[2] Spellberg B, et al. Clin Inf Dis. 2008;47:S249-265.
[3] Fleming TR, Powers JH. Clin Inf Dis. 2008;47:S108-200.
[4] FDA Briefing document, Anti-Infective Drugs Advisory Committee, June 2, 2009. http://www.fda.gov/downloads/AdvisoryCommittees/ CommitteesMeetingMaterials/Drugs/Anti-InfectiveDrugsAdvisoryCommittee/UCM161847.pdf. 
[5] FDA Briefing document, Anti-Infective Drugs Advisory Committee, July 19, 2008. http://www.fda.gov/ohrms/dockets/ac/08/briefing/2008-4364b1-01-FDA.pdf.
[6] National Center for Health Statistics. Deaths: Final Data for 2006. http://www.cdc.gov/NCHS/data/nvsr/nvsr57/nvsr57_14.pdf.
[7] Ochoa-Gondar O, et al. BMC Public Health. 2008;8:222.

 

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