Thursday, January 11, 2018

Statistician's nightmare - mistakes in statistical analyses of clinical trials

Statistician’s job could be risky too.

In recent news announcement, sponsor had to disclose the errors in statistical analyses. All these errors have consequences to the company’s value or even the company’s fate. I hope that the study team members who made this kind of mistakes still have a job in their company. I did have a friend ending up losing the job due to the incorrect report of the p-value.

Here are two examples. In the first example, the p-value was incorrectly calculated and announced, the later had to be corrected – very embarrassing for the statistician who made this mistake. In the second example, the mistake is more on the programming and data management side. Had the initial results been positive, the sponsor might never go back to re-assess the outcomes and the errors might never be identified.

Example #1:
Axovant Sciences (NASDAQ:AXON) today announced a correction to the data related to the Company’s investigational drug nelotanserin previously reported in its January 8, 2018 press release. In the results of the pilot Phase 2 Visual Hallucination study, the post-hoc subset analysis of patients with a baseline Scale for the Assessment of Positive Symptoms - Parkinson's Disease (SAPS-PD) score of greater than 8.0 was misreported. The previously reported data for this population (n=19) that nelotanserin treatment at 40 mg for two weeks followed by 80 mg for two weeks resulted in a 1.21 point improvement (p=0.011, unadjusted) were incorrect. While nelotanserin treatment at 40 mg for two weeks followed by 80 mg for two weeks did result in a 1.21 point improvement, the p-value was actually 0.531, unadjusted. Based on these updated results, the Company will continue to discuss a larger confirmatory nelotanserin study with the U.S. Food and Drug Administration (FDA) that is focused on patients with dementia with Lewy bodies (DLB) with motor function deficits. The Company may further evaluate nelotanserin for psychotic symptoms in DLB and Parkinson’s disease dementia (PDD) patients in future clinical studies.
Example #2:  
(note: PE: pulmonary exacerbation; PEBAC: pulmonary exacerbation blinded adjudication committee) 
Re-Assessment of Outcomes
Following database lock and unblinding of treatment assignment, the Applicant performed additional data assessments due to errors identified in the programming/data entry that impacted identification of PEs. This led to changes in the final numbers of PEs. Based on discussion the Applicant had with the PEBAC Chair, it was decided that 10 PEs initially adjudicated by the PEBAC were to be re-adjudicated by the PEBAC using complete and final subject-level information. This led to a re-adjudication by the PEBAC who were blinded to subject ID, site ID, and treatment. Result(s) of prior adjudication were not provided to the PEBAC.
 Efficacy results presented in Section 7.3 reflect the revised numbers. Further details regarding the reassessment by the PEBAC are discussed in Section 7.3.6.
7.3.6 Primary Endpoint Changes after Database Lock and Un-Blinding
Following database lock and treatment assignment un-blinding, the Applicant performed additional data assessments leading to changes in the final numbers of PEs. Specifically, per the Applicant, during a review of the ORBIT-3 and ORBIT-4 data occurring after database locking and data un-blinding (for persons involved in the data maintenance and analyses), ‘personnel identified errors in the programming done by Accenture Inc. (data analysis contract research organization (CRO)) and one data entry error that impacted identification of PEs. Because of the programming errors, the Applicant states that they chose to conduct a ‘comprehensive audit of all electronic Case Report Forms (eCRFs) entries for signs, symptoms or laboratory abnormalities as entered in the PE worksheets for all patients in ARD-3150-1201 and ARD-3150-1202’ (ORBIT-3 and ORBIT-4). From this audit, the Applicant notes ‘that no further programming errors’ were identified but instead 10 PE events (three from ORBIT-4 and seven from ORBIT-3) were found for which the PE assessment by the PEBAC was considered potentially incorrect. This was based on the premise that subject-level data provided to the PEBAC during the original PE adjudication were updated at the time of the database lock. Reasons provided are: 1) the clinical site provided update information to the eCRF after
 the initial PEBAC review (2 PEs), 2) incorrect information was supplied to the PEBAC during initial adjudication process (2 PEs), 3) inconsistency between visit dates and reported signs and symptoms (6 PEs). After discussion with the PEBAC Chair, it was decided that these 10 PEs initially deemed PEs by the PEBAC were to be re-assessed by the PEBAC using complete and final subject-level information. This led to a re-adjudication by the PEBAC during a closed session on January 25, 2017. This re-adjudication was coordinated by Synteract (Applicant’s CRO) who provided data to the PEBAC that were blinded to subject ID, site ID, and treatment. In addition, result(s) of prior adjudication were not provided. While the PEBAC was provided with subject profiles for other relevant study visits, the PEBAC focus was only on the selected visits for which data were updated or corrected.
 Because of the identified programming errors and PEBAC re-adjudication, there were two new first PEs added to the Cipro arm in ORBIT-3 and two new first PEs added to the placebo arm in ORBIT-4. Given these changes, the log-rank p-value in ORBIT-4 changed from 0.058 to 0.032 (when including sex and prior PEs strata). The p-value in ORBIT-3 changed from 0.826 to 0.974 remaining insignificant. These changes are summarized in Table 9. Note that there were no overall changes in the results of the secondary endpoints analyses from changes in PE status described above.

It is inevitable to make mistakes during the statistical analysis if there is no adequate procedures to prevent them. The following procedures can minimize the chances of making the mistakes as the examples above. 
  • Independent validation process (double programming): The probability for two independent people to make the same mistake is very very low. 
  • Dry-run process: using the dirty data, perform the statistician analysis using the dummy randomization schedule, i.e., perform the statistical analysis with the real data, but fake treatment assignment. The purpose is to do the programming work up front and to check the data upfront so that the issues and mistakes can be identified and corrected. 

Tuesday, January 02, 2018

Adverse Event Collection: When to Start and When to Stop?

In clinical trials, the most critical safety information is the adverse event (AE). There are numerous guidance and guidelines regarding the AE collection. However, there are still a lot of confusions. The very basic question is when to start the AE collection and when to stop the AE collection. For example, here are some discussions:

When to start the AE collection?

It is a very common practice in industry-sponsored clinical trials that AE record keeping begin after informed consent. Adverse events will be collected even for those patients who signed informed consent, but subsequently failed the inclusion/exclusion criteria during the screening period. If we attend the GCP training, it is very likely we will be told this is the way we are supposed to do for adverse event collection in order to be compliant with GCP.

However, the AE definition in the ICH E2A guidance document suggests that adverse event can be recorded at or after the first treatment, not the signing of the informed consent form (ICF). The ICH E2A defined the AE as:
Adverse Event (or Adverse Experience) Any untoward medical occurrence in a patient or clinical investigation subject administered a pharmaceutical product and which does not necessarily have to have a causal relationship with this treatment. An adverse event (AE) can therefore be any unfavourable and unintended sign (including an abnormal laboratory finding, for example), symptom, or disease temporally associated with the use of a medicinal product, whether or not considered related to the medicinal product.
A. Commonly, the study period during which the investigator must collect and report all AEs and SAEs to the sponsor begins after informed consent is obtained and continues through the protocol-specified post-treatment follow-up period. Since the ICH E2A guidance document defines an AE as “any untoward medical occurrence in a patient or clinical investigation subject administered a pharmaceutical product…” This definition clearly excludes the period prior to the IMP’s administration (in this context a placebo comparator used in a study is considered an IMP. Untoward medical occurrences in subjects who never receive any study treatment (active or blinded) are not treatment emergent AEs and would not be included in safety analyses. Typically, the number of subjects “evaluable for safety” comprises the number of subjects who received at least one dose of the study treatment. This includes subjects who were, for whatever reason, excluded from efficacy analyses, but who received at least one dose of study treatment.
 There are situations in which the reporting of untoward medical events that occur after informed consent but prior to the IMP’s administration may be mandated by the protocol and/or may be necessary to meet country-specific regulatory requirements. For example, it is considered good risk management for sponsors to require the reporting of serious medical events caused by protocol-imposed screening/diagnostic procedures, and medication washout or no treatment run-in periods that precede IMP administration. For example, a protocol-mandated washout period, during which subjects are taken off existing treatments (such as during crossover trials) that they are receiving before the test article is administered, may experience withdrawal symptoms from removal of the treatment and must be monitored closely. If the severity and/or frequency of AEs occurring during washout periods are considered unacceptable, the protocol may have to be modified or the study halted. Some protocols may also require the structured collection of signs and symptoms associated with the disease under study prior to IMP administration to establish a baseline against which post-treatment AEs can be compared. In some countries, regulatory authorities require the expedited reporting of these events to assess the safety of the human research.
For a specific study, the screening procedure and the potential injury of the screening procedure should be considered when deciding when to start the AE collection. For a study with very minimal or routine screening procedure (such as phase I study / clinical pharmacology study in healthy volunteers at phase I clinic), it may be ok to collect the AE starting from the first treatment.  For a study with comprehensive screening procedures or with invasive screening procedures, it is advised that the AE collection should start once the subject signs the ICF. For example, in a study assessing the effect of a thrombolytic agent in ischemic stroke patients, the screening procedures include CT scan and arteriogram to assess the location and size of the clot – which can cause adverse effects / injuries to the study participants. In this situation, it is strongly advised that the AE is collected at the ICF signing.

If the AE is collected from the ICF signing, during the statistical analysis, the AEs can be divided into non-treatment emergent AE and treatment emergent AEs (TEAE). Non-TEAEs are those AEs occurred prior to the first study treatment and TEAEs are those AEs with onset date/time at or after the first study treatment. Non-TEAE and TEAE will be summarized separately and the extensive safety analyses will be mainly based on the TEAE.

When to Stop the AE collection?

It is even more murky in terms of when to stop the AE collection because the end of the study is trickier than the start of the study. A study may have a follow-up period after the completion of the study treatment. A subject may discontinue the study treatment earlier, but remain in the study to the end.

There is no clear guidance how long after the last study treatment the AEs need to be collected. In practice, it is common to continue reporting AEs following the last study treatment – the period for post study treatment may be 7 days following the last treatment or 30 days following the last treatment.  The decision of AE collection during the follow-up period should be based on the half life of the study drug, whether there are AEs of special interest related to the study drug in investigation, and whether it is in pediatric or adult population.   

In oncology clinical trials, it is typical not to collect the adverse events during the long-term follow-up period. Adverse events may just be collected for short period after the last treatment, for example 30 days or 3 months or 6 months following the last study treatment. During the long-term follow-up period, only the study endpoint (tumor related events) such as death, tumor progression, or secondary malignant event will be collected.

Should adverse events be collected for subjects who discontinued the study treatment earlier? There is a good question and answer discussion at firstclinica.comAE Reporting for Discontinued Patient
QUESTION: What are the investigator's responsibilities in terms of reporting the post-discontinuation adverse events? On one hand, since the patient discontinued from the study, some think that the investigator has no right to review the patient's clinical record under HIPAA (authorization terminated) or informed consent regulations (consent withdrawn) and consequently has no authority or responsibility to report the adverse events. On the other hand, there does not appear to be any variances to an investigator's IND obligations (even when a patient discontinues from the study) with respect to reporting adverse events according to 21 CFR 312.64. Also, would the investigator's reporting responsibilities be the same for Situation A and Situation B?
FDA has stated that clinical investigators need to capture information about adverse effects resulting from the use of investigational products, whether or not they are conclusively linked to the product. The fact that a subject has voluntarily withdrawn from the study does not preclude FDA's need for such information. In fact, withdrawal is often due to adverse effects, some already realized and others beginning and that will later progress. For your first scenario, that is obviously not a real problem since the investigator is also the individual's private physician and obviously has this information. While you are correct to worry about privacy issues in both scenarios, the public welfare is a larger issue. Failure to capture and report adverse effects, particularly serious adverse effects, will not only be a problem for the individual in question but potentially for other actual and potential study subjects. It is also essential to capture the information so that the total picture is available to FDA when a marketing decision is imminent. The individual in question may be one of very few who would evidence the particular adverse effect, particularly given the limited number of individuals included in a study. However, this information could have major ramifications for the potentially large population of users of the drug once legally marketed. How to best go about collecting the details of the adverse effect is obviously a different issue.
In summary, the AE collection can be depicted as the following where TEAE stands for treatment-emergent adverse event:

Saturday, December 23, 2017

Composite Endpoint and Competing Risk Model

A competing risk is an event whose occurrence precludes the occurrence of the primary event of interest. For example, when the primary outcome is death due to cardiovascular causes, then death due to non-cardiovascular causes serves as a competing risk, because subjects who die of non-cardiovascular causes (e.g., death due to cancer) are no longer at risk of death due to a cardiovascular cause. However, when the primary outcome is all-cause mortality, then competing risks are absent, as there are no events whose occurrence precludes the occurrence of death due to any cause. In event-driven clinical trials, if a study subject drops out from the study prior to occurrence of the event in interest, the event of dropout precludes the occurrence of the event in interest, this is also a competing risk.

Competing risk issue occurs in clinical trials with a composite endpoint or an endpoint with composite outcome. A composite outcome consists of two or more component outcomes. Patients who have experienced any one of the events specified by the components are considered to have experienced the composite outcome. The main advantages supporting the use of a composite outcome are that it increases statistical efficiency because of higher event rates, which reduces sample size requirement, costs, and time; it helps investigators avoid an arbitrary choice between several important outcomes that refer to the same disease process; and it is a means of assessing the effectiveness of a patient reported outcome that addresses more than one aspect of the patient’s health status
It is common to use a composite endpoint in clinical trials, especially in clinical trials where the primary interest is to reduce the adverse outcomes, but the occurrence of these adverse outcomes may not be frequent enough. If we do a study with each individual component as the endpoint, the sample size required will be too large.

MACE (major adverse cardiac events) is a composite endpoint frequently used in clinical trials assessing the treatment effect in cardiac health. MACE is defined as any event of all-cause mortality, myocardial infarction, or stroke. If a patient died during the study, the MI or stroke will not be observed. If a MI or Stroke event occurred and the subject is discontinued from the study once one of these events occurred, the death event will not be observed – one component is a competing risk for another component.
In clinical trials in pulmonary arterial hypertension, the composite endpoint is used to evaluate the treatment effect in reducing the mortality and morbidity events. EMA guidance “GUIDELINE ON THE CLINICAL INVESTIGATIONS OF MEDICINAL PRODUCTS FOR THE TREATMENT OF PULMONARY ARTERIAL HYPERTENSION “ suggested the time to clinical worsening as the primary efficacy endpoint where the clinical worsening is defined as a composite endpoint consisting of:
1. All-cause death.
2. Time to non-planned PAH-related hospitalization.
3. Time to PAH-related deterioration identified by at least one of the following parameters:
  • increase in WHO FC;
  • deterioration in exercise testing
  • signs or symptoms of right-sided heart failure

Arterial Hypertension”, the primary end point in a time-to-event analysis was a composite of death or a complication related to pulmonary arterial hypertension, whichever occurred first, up to the end of the treatment period. The composite endpoint includes the following events:
  • death (all-cause mortality)
  • hospitalization for worsening of PAH based on criteria defined in the study protocol
  • worsening of PAH resulting in need for lung transplantation or balloon atrial septostomy initiation of parenteral (subcutaneous or intravenous) prostanoid therapy or chronic oxygen therapy due to worsening of PAH
  • disease progression (patients in modified NYHA/WHO functional class II or III at Baseline) confirmed by a decrease in 6MWD from Baseline (≥ 15%, confirmed by 2 tests on different days within 2 weeks) and worsening of NYHA/WHO functional class
  • disease progression (patients in modified NYHA/WHO functional class III or IV at Baseline) confirmed by a decrease in 6MWD from Baseline (≥ 15%, confirmed by 2 tests on different days within 2 weeks) and need for additional PAH-specific therapy.

There is a competing risk issue here, for example, lung transplantation and death are competing each other. If patient has a lung transplantation, the disease course will be changed, and the chance of death and occurrence of other events will be altered. 

A common approach to avoid the competing risk issue is to analyze the time to first event (any one of the components defined in the composite endpoint) as the primary efficacy endpoint even though this approach is often criticized because the importance / severity of these components is not equal (death should be given way more weight than other non-fatal events). FDA seems to be totally comfortable with the time to first event approach in both composite endpoint situation (as evidenced by the approval ofSelexipeg) and recurrent event situation (as evidenced by the FDA advisorycommittee meeting discussion). In a panel discussion at the regulatory-industry workshop in 2017 on the topic of Better Characterization of Disease Burden by Using Recurrent Event Endpoints (View Presentation), Drs Bob Temple and Norman Stockbridge both commented that FDA is fine with the time to fist event analysis as long as further analyses  are performed to evaluate the treatment effect on each individual component.

Competing risk model may be used in statistical analysis of the clinical trial data either as the primary method or as sensitivity analysis. In Schaapveld et al (2015) Second Cancer Risk Up to 40 Years after Treatment for Hodgkin’s Lymphoma, the competing risk model was used for analyzing the cumulative incidence of second cancers.
The cumulative incidence of second cancers was estimated with death treated as a competing risk, and trends over time were evaluated in competing-risk models, with adjustment for the effects of sex, age, and smoking status when appropriate

Competing risk model is more likely to be used as a sensitivity analysis, for example, in SPRINT study “A Randomized Trial of Intensive versus Standard Blood-Pressure Control”, The Fine–Gray model for the competing risk of death was used as a sensitivity analysis.

There are quite some discussions about the competing risk model in clinical trials:

In the situation where there is a competing risk issue, the Grey’s method or Fine and Gray method can be used. These methods are based on the paper below:
  • Gray, R. J. (1988), “A Class of K-Sample Tests for Comparing the Cumulative Incidence of a Competing  Risk,” Annals of Statistics, 16, 1141–1154.
  • Fine, J. P. and Gray, R. J. (1999), “A Proportional Hazards Model for the Subdistribution of a Competing Risk,” Journal of the American Statistical Association, 94, 496–509.

There are SAS macros for Gray’s method. Recently, Gray’s method and Fine and Gray methods are built in SAS PHREG and SAS PHREG can be handily used for performing the competing risk model. Here are some SAS papers regarding competing risk model analysis.

Sunday, December 10, 2017

Recurrent Events versus Composite Events: Statistical Analysis Methods for Recurrent Events

Recurrent events are repeated occurrences of the same type of event.
Composite endpoint is a combination of various clinical events that might happen, such as heart attack or death or stroke, where any one of those events would count as part of the composite endpoint.

While composite endpoint may also be discussed within the scope of the recurrent event endpoint, there are some distinctions between these two terms. The methods for statistical analysis are also different:
Recurrent Event Endpoint
Composite Endpoint
  • Relapses in multiple sclerosis
  • Exacerbations in pulmonary diseases such as chronic obstructive pulmonary disease
  • Bleeding episodes in hemophilia

  • MACE in cardiovascular trials where MACE (major adverse cardiac event) includes death, MI, and stroke.
  • Clinical worsening event in pulmonary arterial hypertension where clinical worsening includes all-cause death, PAH-related hospitalization, PAH-related deterioration of disease,…

Same type of event
Different type of event
Each event has the same contribution to the total number of events.
It is usually criticized that each component may contribute differently to the total counts (death is much severe event comparing with others)
The study design is usually with fixed duration. Events are collected over a fixed duration of time
The study design is usually an event-driven study. Different subjects may be followed up for different durations
Usually for events with relatively frequency
Usually for events that not frequently or rarely happen (so that we combine all these types to increase the power and minimize the sample size)
Can be analyzed as:
Frequency of events
Annualized rate of events
Time to first event
Duration of events
Duration of event free
Can be analyzed:
Time to the first event
Time to event for each component
Frequency of events
Competing risk is less an issue
Competing risk is an issue
Example of a trial with recurrent event endpoint:
Example of a trial with composite endpoint:

While the composite endpoint is usually analyzed as time to first event (whichever occurs the first for any of the components) using log rank test or Cox proportional hazard model, the recurrent event may be analyzed using different ways. Below are some examples of  

Emicizumab Prophylaxis in Hemophilia A with Inhibitors

The primary end point was the difference in the rate of treated bleeding events (hereafter referred to as the bleeding rate) over a period of at least 24 weeks between participants receiving emicizumab prophylaxis (group A) and those receiving no prophylaxis (group B) after the last randomly assigned participant had completed 24 weeks in the trial or had discontinued participation, whichever occurred first.
For all bleeding-related end points, comparisons of the bleeding rate in group A versus group B and the intraindividual comparisons were performed with the use of a negative binomial-regression model to determine the bleeding rate per day, which was converted to an annualized bleeding rate.
The primary efficacy end point was the annual rate of sickle cell–related pain crises, which was calculated as follows: total number of crises× 365 ÷ (end date − date of randomization + 1),with the end date defined as the date of the last dose plus 14 days. Annualized rates were used for the comparisons because they take into account the duration that a participant was in the trial. The crisis rate for every patient was annualized to 12 months. The annual crisis rate was imputed for patients who did not complete the trial. The difference in the annual crisis rate between the high-dose crizanlizumab group and the placebo group was analyzed with the use of the stratified Wilcoxon rank-sum test, with the use of categorized history of crises in the previous year (2 to 4 or 5 to 10 crises) and concomitant hydroxyurea use (yes or no) as strata. A hierarchical testing procedure was used (alpha level of 0.05 for high-dose crizanlizumab vs. placebo, and if significant, low-dose crizanlizumab vs. placebo).

A painful crisis was defined as a visit to a medical facility that lasted more than four hours for acute sickling-related pain (hereinafter referred to as a medical contact), which was treated with a parenterally administered narcotic (except for a few facilities in which only orally administered narcotics were used); the definition is similar to that used in a previous study. Annual rates were computed by dividing the number of crises by the number of years elapsed (e.g., 6 crises in 1.9 years - 3.16 crises per year). To test the effect of treatment on the crisis rate, the patients were ranked according to the number of crises they had had per year for observed periods of up to two years. Death was considered the worst outcome, followed by a stroke (defined as a documented new neurologic deficit lasting more than 24 hours, confirmed by a neurologist) or the institution of long-term transfusion therapy (more than four months); outcomes for all other patients were ranked according to the individual crisis rate. These ranks were used to compare the two treatment groups (Van der Waerden’s test). A rank statistic was planned for the primary analysis because it was expected to have more power to detect differences and to be less influenced by extreme values than a t-test of the means.

The primary efficacy endpoint was mean change from baseline in frequency of headache days for the 28-day period ending with week 24. A headache day was defined as a calendar day (00:00 to 23:59) when the patient reported four or more continuous hours of a headache, per the patient diary. Subsequent to study initiation, but prior to study completion and treatment unmasking, the protocol and statistical analysis plan for PREEMPT 2 was amended to change the primary and secondary endpoints, making frequency of headache days the PREEMPT 2 primary endpoint. This change was made based on several factors: availability of PREEMPT 1 data, guidance provided in newly issued International Headache Society clinical trial guidelines for evaluating headache prophylaxis in CM (34) and the earlier expressed preference of the US Food and Drug Administration (FDA), all of which supported using headache day frequency as a primary outcome measure for CM. For each primary and secondary variable, prespecified comparisons between treatment groups were done by analysis of covariance of the change from baseline, with the same variable’s baseline value as a covariate, with main effects of treatment group and medication overuse strata. The baseline covariate adjustment was prespecified as the primary analysis; sensitivity analyses (e.g., rank-sum test on changes from baseline without a baseline covariate) were also performed.

The primary outcome was the time to the first acute exacerbation of COPD, with acute exacerbation of COPD defined as “a complex of respiratory symptoms (increased or new onset) of more than one of the following: cough, sputum, wheezing, dyspnea, or chest tightness with a duration of at least 3 days requiring treatment with antibiotics or systemic steroids.” The primary analysis was based on a log-rank test of the difference between the two treatment groups in the time to the first exacerbation, with no adjustments for baseline covariates. A Cox proportional-hazards  model was used to adjust for differences in prespecified, prerandomization factors that might predict the risk of acute exacerbations of COPD.

The primary outcome was the effect of simvastatin on the exacerbation rate, which was defined as the number of exacerbations per person-year.

COPD exacerbation rates in the two study groups were compared with the use of a rate ratio. The independence of individual exacerbations was ensured by considering participants to have had two separate exacerbations if the onset dates were at least 14 days apart. Exacerbation rates in each group and the between-group differences were analyzed with the use of negative binomial regression modeling and time-weighted intention-to-treat analyses with adjustments of confidence intervals for between-participant variation (overdispersion).

FDA recommended the time to first exacerbation as the primary efficacy endpoint over the use of frequency of exacerbations as primary endpoints. The time to first exacerbation will be analyzed using log-rank test or Cos proportional hazard model.
Even though the FDA agrees that the frequency of exacerbations may be a clinically relevant endpoint; however, there are several statistical issues and challenges in providing a reliable and unbiased estimate of treatment effect using this endpoint:
  • Dependencies of exacerbation on previous exacerbations within patients
  • Effect of influential cases as it can potentially impact the results
  • Distinguishing between early vs. late exacerbations as a function of time
  • Distinguishing between first vs. subsequent exacerbations within patients
  • Investigator biases in assessing the number of events (e.g. events occurring close together)

Tuesday, November 28, 2017

Bonferroni method, alpha level partition, and gatekeeper hierarchical test strategy in Bronchiectasis clinical trials

In a recent FDA advisory committee meeting in November 16, 2017, we learned the first hand application of the various approaches for multiplicity adjustment: Single step Bonferroni method, Single step arbitrary partition of alpha level, gatekeeping - hierarchical test procedure which was discussed in one of my previous posts.

During this meeting of the Antimicrobial Drugs Advisory Committee (AMDAC), the committee considered new drug application (NDA) 209367 for ciprofloxacin dry powder for inhalation (DPI), sponsored by Bayer HealthCare Pharmaceuticals, Inc. The drug is being proposed for the reduction of exacerbations in non-cystic fibrosis bronchiectasis (NCFB) adult patients (≥18 years of age) with respiratory bacterial pathogens.

The clinical program to evaluate the safety and efficacy of ciprofloxacin DPI consisted of 2 nearly identical phase 3, randomized, multicenter, placebo-controlled trials known as RESPIRE 1 and RESPIRE 2. See table 1 below for the design information.

For both RESPIRE 1 and RESPIRE 2 studies, the primary efficacy endpoint is time to first exacerbation. Within each study, there are three treatment arms with two hypothesis tests. In order to maintain the blinding, the placebo arm is further divided into placebo for 28 days on/off treatment regimen and 14 days on/off treatment regimen. However, for analysis purpose, the placebo groups are pooled. The list of hypothesis testing and the allocated alpha are listed below. For RESPIRE 1 study, the alpha level of 0.025 for each hypothesis test is based on Bonferroni method for multiplicity adjustment. For RESPIRE 2 study, the alpha level of 0.001 and 0.049 is based on the arbitrary partition (as long as the total alpha = 0.05).  

RESPIRE 1 Study (Bonferroni method for multiplicity adjustment):
Hypothesis 1: ciprofloxacin DPI for 28 days on/off treatment regimen versus pooled placebo (alpha=0.025)
Hypothesis 2: ciprofloxacin DPI for 14 days on/off treatment regimen versus pooled placebo (alpha=0.025)
RESPIRE 2 Study (arbitrary partition of alpha level for multiplicity adjustment):
Hypothesis 1: ciprofloxacin DPI for 28 days on/off treatment regimen versus pooled placebo (alpha=0.001)
Hypothesis 2: ciprofloxacin DPI for 14 days on/off treatment regimen versus pooled placebo (alpha=0.049)
The study results indicate some efficacy, but not consistent across all four hypothesis tests. For details about the study results, please see FDA's advisory committee briefing bookstudy results for RESPIRE 1, and study results for RESPIRE 2 on

The study also included a long list of the secondary efficacy endpoints. To control the overall type I error rate associated with testing primary and secondary endpoints in two treatment regimens (Cipro 14 and Cipro 28) against placebo, separate hierarchical testing sequences of primary, key secondary and other secondary endpoints were pre-specified for each regimen with statistical testing at α=0.025 for each Cipro arm in RESPIRE 1 and α=0.001 for Cipro 28 and α=0.049 for Cipro 14 in RESPIRE 2. If the primary endpoint was significant for a Cipro regimen then the next endpoint in the sequence (i.e., key secondary endpoint) was tested within that Cipro regimen. Statistical testing would only continue to the next endpoint in the hierarchy if the preceding endpoint in the hierarchy showed significance. Endpoints which could not be statistically tested were considered to be exploratory. The hierarchical testing strategy is shown in Figure 2.

Unfortunately, the hierarchical strategy did not work well and majority of the secondary endpoints were not tested because the insignificant results in primary efficacy endpoints. As mentioned in FDA's briefing book:
Under the pre-specified hierarchical strategy, confirmatory testing of the first secondary endpoint (frequency of exacerbations) against Pooled Placebo, and all subsequent endpoints, could not be performed for Cipro 28 (both trials) and for Cipro 14 (RESPIRE 2) because the respective findings for the primary endpoint of TFE were not significant. In RESPIRE 1, confirmatory testing of Cipro 14 could only be performed up to the first secondary endpoint (FOE) which failed to show significance. With the exception of a statistically significant finding observed for one comparison (i.e., Cipro 14 day vs. Pooled Placebo for the primary endpoint in RESPIRE 1), all other comparisons were considered to be exploratory or not statistically significant. As indicated in Figure 2 there was the potential for up to 32 comparisons to show statistical significance (8 endpoints in each of two Cipro arms across two trials).
FDA advisory committee was not convinced by the evidence of the ciprofloxacin DPI efficacy. Here is the voting result. It is unlikely for FDA to approve a product with such a voting result even though there is currently no approved drug for treating non-cystic fibrosis bronchiectasis.

Had a different study design and different method for multiplicity adjustment been used, the situation might be very different. The evidence for the experimental drug might be more obvious if a simpler study design was used - at least this is the situation for 14 day on/off regimen versus placebo.

We are now closely watching the fate of Aradigm's NDA for Ciprofloxacin in treating non-CF bronchiectasis. Aradigm's pivital studies (Orbit 3 and Orbit 4) are simpler in study design with one of two studies positive. One thing is for sure: there will not be the complicated situations in dealing with the multiplicity adjustment. 


Saturday, November 25, 2017

Co-primary endpoints and multiple primary endpoints

In recent FDA guidance 'Multiple Endpoints in Clinical Trials' and EMA guidance 'Guideline on multiplicity issues in clinical trials', the term 'co-primary endpoints' and 'multiple primary endpoints' are clarified.

Historically, the term 'co-primary endpoints' was used for different meanings in different clinical trial protocols, statistical analysis plans, and journal articles. In many cases, the term 'co-primary endpoints' was inappropriately used for really 'multiple primary endpoints'.

Co-primary endpoints should only be used when there are more than one primary endpoint and declare the study success only if both primary endpoints are statistically significant in favor of the experimental treatment. When co-primary endpoints are used, each primary endpoint is tested at significant level of 0.05. There is no multiplicity issue involved.

In contrary, the term 'multiple primary endpoints' should be used if there are more than one primary endpoint and declare the study success if either one of the primary endpoints is statistically significant in favor of the experimental treatment. In this case, each primary endpoint is tested at a significant level determined by the method for multiplicity adjustment or simply by the partition of the alpha levels.

Here is what EMA guidance 'guideline on multiplicity issues in clinical trials' says:
If more than one primary endpoint is used to define study success, this success could be defined by a  positive outcome in all endpoints or it may be considered sufficient, if one out of a number of endpoints has a positive outcome. Whereas in the first definition the primary endpoints are designated  as co-primary endpoints, the latter case is different and would require appropriate adjustment for multiplicity. More generally, in case of more than two primary endpoints, adjustment is needed if not all endpoints need to be significant to define study success, and the inability to exclude deteriorations in other primary endpoints would have to be considered in the overall benefit/risk assessment.
In FDA's guidance 'multiple endpoints in clinical trials', the term 'co-primary endpoints' was extensively discussed and the examples of co-primary endpoints were provided. In section C of the guidance, it says:
For some disorders, there are two or more different features that are so critically important to the disease under study that a drug will not be considered effective without demonstration of a treatment effect on all of these disease features. The term used in this guidance to describe this circumstance of multiple primary endpoints is co-primary endpoints. Multiple primary endpoints become co-primary endpoints when it is necessary to demonstrate an effect on each of the endpoints to conclude that a drug is effective.
The guidance provided the following examples of co-primary endpoints where both co-primary endpoints needed to be statistically significant in order to declare the trial success:

  • A recent approach to studying treatments is to consider a drug effective for migraines only if pain and an individually-specified most bothersome second feature are both shown to be improved by the drug treatment. 
  • Drugs for Alzheimer’s disease have generally been expected to show an effect on both the defining feature of the disease, decreased cognitive function, and on some measure of the clinical impact of that effect. Because there is no single endpoint able to provide convincing evidence of both, co-primary endpoints are used. One primary endpoint is the effect on a measure of cognition in Alzheimer’s disease (e.g., the Alzheimer’s Disease Assessment Scale-Cognitive Component), and the second is the effect on a clinically interpretable measure of function, such as a clinician’s global assessment or an Activities of Daily Living Assessment.
In an article by Kantarjian et al “Decitabine improves patients outcome in myelodysplastic syndromes: results of a phase III randomized study”, the term ‘coprimary endpoints’ was incorrectly used for ‘multiple endpoints’ even though the multiplicity adjustment method (Bonferroni correction) was appropriately applied.

The coprimary endpoints in the current study were ORR and time to AML transformation or death. Response was assessed according to the International Working group (IWG) criteria……Two analyses, one interim and one final, were planned using the stopping rules of O’Brien and Fleming. The overall type 1 error rate was maintained at a maximum of 5% by applying a Bonferroni correction for the coprimary endpoints at the final analysis. A maximum P value of .024 was required to establish statistical significance using a 2-sided analysis for either of the coprimary endpoints (ORR or time to AML or Death).

In an article by McLaughlin et al "Bosentan added to sildenafil therapy inpatients with pulmonary arterialhypertension", the term of co-primary endpoints was used for a situation that 'multiple endpoints' should be used. Noticed that the original protocol used a study design with two primary endpoints with partition of alpha-level (0.04 for time to morbidity/mortality and 0.01 for change in 6MWD) as an approach for multiplicity adjustment. 
The initial assumptions for the primary end-point were an annual rate of 21% on placebo with a risk reduced by 36% (hazard ratio (HR) 0.64) with bosentan and a negligible annual attrition rate. In addition, it was planned to conduct a single final analysis at 0.04 (two-sided), taking into account the existence of a co-primary end-point (change in 6MWD at 16 weeks) planned to be tested at 0.01 (two-sided). Over the course of the study, a number of amendments were introduced based on the evolution of knowledge in the field of PAH, as well as the rate of enrolment and blinded evaluation of the overall event rate. On implementation of an amendment in 2007, the 6MWD end-point was changed from a co-primary end-point to a secondary endpoint and the Type I error associated with the single remaining primary end-point was increased to 0.05 (two-sided).

Friday, November 03, 2017

SAD and MAD: Single Ascending Dose and Multiple Ascending Dose first-in-human studies

The acronym is everywhere in clinical trials. Previously I mentioned that in 21st Century Cure Act, an acronym RAT was used for Regnerative Advanced Therapy designation – the term ‘RAT’ was criticized and later was changed to MRAT(Regenerative Medicine Advanced Therapy) in FDA’s implementations.

Now we have a pair of names SAD and MAD commonly used in early phase clinical trials. It does not mean anybody will be sad or mad. A sponsor should be happy (not SAD or MAD) when its development program can progress into the clinical trial stage.
SAD stands for single ascending dose and MAD stands for multiple ascending dose. SAD and MAD studies are typically the first-in-human (FIH) studies. They seek to gain information on safety and tolerability, general pharmacokinetic (PK), and pharmacodynamic (PD) characteristics, and identify the maximum tolerated dose (MTD). SAD/MAD study can also be used to test the cardiac safety and evaluate QT/QTc prolongations.

There may be a lot of dose escalation studies that belong to SAD and MAD studies even though the SAD/MAD terms are not used. For example, the popular 3+3 design is one type of the SAD/MAD study with focuses on safety and tolerability.  

SAD/MAD studies are usually conducted in healthy volunteers in clinical research unit (CRU) or phase I unit. But they can be conducted in patients when it is unethical to test the experimental drug (for example, the oncology drugs and plasma-derived drugs) in healthy volunteers. SAD/MAD studies can be combined into one study within the same study protocol or conducted as two separate studies.

For SAD studies, the starting dose is based on the pre-clinical and animal studies. For MAD studies, the starting dose is usually based on results from the SAD study.

From the PK assessment standpoint, in SAD studies, each subject receives a single dose and the series PK samples can be taken to evaluate the PK profiles after single dose. The study will be conducted on cohort basis. Subjects within each cohort receive the same level of dose. In MAD studies, each subject receives multiple doses. After the steady state is achieved, the series PK samples will be taken to evaluate the PK profiles at the steady state. The study is conducted on cohort basis. Subjects within each cohort will receive the same level of dose. With the PK results from SAD/MAD studies, dose linearity and dose proportionality can be evaluated.   

From the safety assessment standpoint, in both SAD/MAD situations, the first cohort of subjects receive the lowest dose (starting dose). Subjects are usually confined in Clinical Research Unit (CRU) with close safety monitoring. After each cohort, safety and tolerability will be assessed to determine if the next cohort with higher dose should be continued. The safety evaluation after each cohort is usually performed by the internal team within the sponsor, but can certainly be performed by the independent committee such as data and safety monitoring committee (DSMB). With the safety data, the maximum tolerated dose (MTD) may be identified.   

In SAD/MAD studies, within each cohort, placebo control can be added. Depending on whether there is a concurrent placebo control group, the SAD/MAD studies could have the following types.
  • SAD without placebo control
  • SAD with placebo control
  • MAD without placebo control
  • MAD with placebo control

When placebo group is added to the SAD/MAD study, to avoid too many subjects in placebo group for the final analysis, it is very common to use a n:1 randomization ratio within each cohort, For the final analysis, subjects in placebo group across all cohorts are pooled together.

Here are a couple of examples for SAD/MAD study designs – they are extracted from a presentation slide I made almost 20 years ago, but is still relevant:

Further Reading/References: