Sample Size Calculation Without Considering Dropout Rate

When planning for clinical trials, sample size calculation is a two-step or three-step process. For clinical trials with continuous variable or categorical variable as primary efficacy endpoint, the sample size calculation is usually a two-step process: the step 1 is to calculate the sample size based on the effect size / standard deviation for continuous variable; difference in rate/proportions and the control group rate/proportion for categorical variable. The step 2 is to apply the dropout rate to calculate the number of subjects needed to be randomized. I had an earlier post “sample size considering the dropout rate” to state that the calculation to account for the dropout rate should be by dividing (1-dropout rate), not by multiplying (1+dropout rate).

For clinical trials with time to event variables, the sample size calculation is usually involved in three steps:

• Step 1: Estimate the number of events needed based on hazard ratio, median survival time, or event rate at a specified time frame
• Step 2: Estimate the number of subjects needed to obtain the required number of events based on the accrual time, the follow-up, or the overall study duration
• Step 3: Estimate the total sample size by considering the dropout rate.

Applying the dropout rate in clinical trials with time to event endpoint is not straightforward. The dropout rate is usually not a constant throughout the study (during the accrual period and during the follow-up period).

To calculate the sample size for studies with time to event variables, I usually use Cytel’s EAST software. To deal with the dropout rate, the EAST software user manual suggests a ‘trial and error’ method. With this method, we will need to provide an initial dropout rate (expressed in ‘probability of dropout’ or ‘hazard for dropout’). We then check the summary of the sample size estimation. The number of dropouts is displayed, and the dropout rate can easily be calculated by dividing the number of dropouts by the number of subjects. If the calculated dropout rate is different from the assumptions, we can then go back to revise the initial input – do this several times until the calculated dropout rate from EAST matches the assumed dropout rate.

I recently run into two scenarios where the sample size calculation does not need to consider the dropout rate.

• Sample size calculation for an animal study (pigs for example) with a time to event variable. The pigs used in the experiment will be confined in a facility. There is no lost-to-follow-up or anything situation like that. There is no need for us to consider the dropout rate if we try to estimate the number of pigs needed for an experiment. 

• Sample size calculation for a metastatic non-small cell lung cancer (NSCLC) study with overall survival as the primary efficacy endpoint. The median survival time for metastatic NSCLC patients is usually short. In other words, the mortality rate for NSCLC patients is high. In this situation, the number of subjects who lost to follow-up is generally small (less than 5%) and we may not need to apply the dropout rate in calculating the number of subjects to be randomized. A friend of mine who is an expert in NSCLC clinical trials told me that in their studies with OS as primary efficacy endpoint, they will calculate the number of death events needed, and then simply add 25-30% more patients on top of the number of death events to account for a small proportion of subjects who may live much longer. For example, based on the hazard ratio, accrual time, and follow-up time, if the calculated number of death events is 200 events, we can simply have a sample size of 250-260 subjects randomized (25-30% more than the number of death events). 

Here are some recent trials from New England Journal of Medicine where there was no mention of dropout rate in sample size calculations:

• Durvalumab after Chemoradiotherapy in Stage III Non–Small-Cell Lung Cancer and the study protocol
• Nivolumab versus Docetaxel in Advanced Squamous-Cell Non–Small-Cell Lung Cancer and the study protocol
• Atezolizumab for First-Line Treatment of Metastatic Nonsquamous NSCLC and the study protocol
• Dimopoulos 2018 Phase 3 Trial of Ibrutinib plus Rituximab in Waldenström’s Macroglobulinemia
• A Randomized, Double-Blind, Placebo-Controlled, Phase 3 Study of Ibrutinib or Placebo in Combination with Rituximab in Subjects with Waldenström’s Macroglobulinemia

• Pembrolizumab plus Chemotherapy in Metastatic Non–Small-Cell Lung Cancer

Expectedness Assessment: Expected / Unexpected Adverse Events and SUSAR

In clinical trials, reporting of adverse events is critical to ensure the safety of participants. When an adverse event is reported, it is also assessed for the severity, seriousness, causality, and outcome. All of these are the standard fields that are supposed to be collected on the case report forms and on serious adverse event (SAE) forms. 

Expectedness of an adverse event is also critical; however, the assessment of expectedness is usually not collected on the case report form or SAE form because the responsibility of the expectedness evaluation is not on investigator’s side, but on the sponsor’s side. SUSAR (suspected unexpected serious adverse reaction) must be reported to regulatory agencies and IRBs in expedited way.

Definition of Expectedness:

According to ICH E2A “CLINICAL SAFETY DATA MANAGEMENT: DEFINITIONS AND STANDARDS FOR EXPEDITED REPORTING”, the unexpected adverse drug reaction is defined as the following:

3. Unexpected Adverse Drug Reaction An adverse reaction, the nature or severity of which is not consistent with the applicable product information (e.g., Investigator's Brochure for an unapproved investigational medicinal product). (See section III.C.)

In each individual study protocol, the definition may be a little bit different, but essentially the same.

Unexpected: – Not listed in Investigator Brochure or is not listed at the specificity or severity that has been observed, or, if an investigator brochure is not required or available, is not consistent with the risk information described in the general investigational plan or elsewhere in the current application.

An unexpected adverse reaction has a nature or severity of which is not consistent with the study intervention description (e.g. Investigator's Brochure for an unapproved investigational product or package insert/summary of product characteristics for an approved product). The unexpected AE must be reported, whether related to the study intervention or not, with as much detail as is available

Expected: - listed in Investigator Brochure.

The Purpose of Expedited Reporting of the Suspected Unexpected Serious Adverse Events (SUSAR)

According to ICH E2A “CLINICAL SAFETY DATA MANAGEMENT: DEFINITIONS AND STANDARDS FOR EXPEDITED REPORTING E2A”, the purpose of the SUSAR reporting is defined as:

C. Expectedness of an Adverse Drug Reaction The purpose of expedited reporting is to make regulators, investigators, and other appropriate people aware of new, important information on serious reactions. Therefore, such reporting will generally involve events previously unobserved or undocumented, and a guideline is needed on how to define an event as "unexpected" or "expected" (expected/unexpected from the perspective of previously observed, not on the basis of what might be anticipated from the pharmacological properties of a medicinal product). As stated in the definition (II.A.3.), an "unexpected" adverse reaction is one, the nature or severity of which is not consistent with information in the relevant source document(s). Until source documents are amended, expedited reporting is required for additional occurrences of the reaction.

The following documents or circumstances will be used to determine whether an adverse event/reaction is expected: 1. For a medicinal product not yet approved for marketing in a country, a company's Investigator's Brochure will serve as the source document in that country. (See section III.F. and ICH Guideline for the Investigator's Brochure.) 2. Reports which add significant information on specificity or severity of a known, already documented serious ADR constitute unexpected events. For example, an event more specific or more severe than described in the Investigator's Brochure would be considered "unexpected". Specific examples would be (a) acute renal failure as a labeled ADR with a subsequent new report of interstitial nephritis and (b) hepatitis with a first report of fulminant hepatitis.

Expectedness/Unexpectedness Not Collected in Case Report Forms or SAE Forms

CDISC/CDASH “Clinical Data Acquisition Standards Harmonization (CDASH) User Guide” excluded the collection of ‘expected criteria’, citing that it is “handled in Clinical Investigative Brochure”



In FDA’s Guidance for Industry and Investigators “Safety Reporting Requirements for INDs and BA/BE Studies”, the reporting responsibility for unexpected adverse events is specified for sponsors (not the investigators). 

Two Types of Unexpectedness and Handling the List of Unexpected AEs

According to a blog post "Seriousness, Expectedness and Investigator Brochures", there are actually two types of unexpectedness 

The first is “regulatory expectedness”. This refers to the SAEs that the company considers likely/possibly or probably related to the study drug. This list is used to determine whether an SAE is a SUSAR (Suspected, unexpected serious adverse reaction) and thus expeditable to FDA, EMA and other health agencies.

The second we can call “clinical expectedness” which is a listing of SAEs that the investigator and patient may encounter during the trial and should be aware of. They may be due to the drug, the disease, comedications, concomitant illnesses (e.g. the flu) or other causes. These may or may not be the same as the “regulatory expectedness” list of SAEs but are important for the treating physician to be aware of and look for. It may not be possible yet to determine whether the particular SAE is due to the drug or the disease or comedications etc. This may become clearer later in the drug’s lifespan as more data becomes available; but sometimes it does not ever become clear.

Due to different understanding of the expectedness, different companies may act differently in handling the expectedness assessment. Some companies (especially the European companies) may want to add as many AEs as possible to the Investigator Brochure so that less AEs would meet the unexpected criteria – specifically the SUSAR criteria for expedite reporting.

Other companies may want to add as few AEs as possible to the Investigator Brochure because two many AEs listed in the Investigator Brochure would give the investigators an impression that the investigational product is not safe.

The right approach should be that the list of AEs/SAEs should be carefully reviewed by one or more medically qualified persons to decide if terms should be included (added) in the Investigator Brochure.

Expectedness assessment is more for fulfilling the sponsor’s reporting responsibility and expected / unexpected AEs are evaluated by the sponsor (not the investigators) through comparing to the Investigator Brochure or product label.

Expected AEs versus AEs of Special Interest (AESI)

Sometimes, the study protocol may include a list of AEs of Special Interest. According to FDA guidance for industry: E2F Development Safety Update Report AEs of Special Interest are defined as following.

“Adverse event of special interest: An adverse event of special interest (serious or non-serious) is one of scientific and medical concern specific to the sponsor’s product or program, for which ongoing monitoring and rapid communication by the investigator to the sponsor can be appropriate. Such an event might warrant further investigation in order to characterize and understand it. Depending on the nature of the event, rapid communication by the trial sponsor to other parties (e.g., regulators) might also be warranted. (Based on CIOMS VI)”

Here are some examples of AESI: distal emboli events in clinical trials using thrombolytic agents, syncope events in pulmonary arterial hypertension studies, diarrhea in Irritable Bowel Syndrome studies) . I had a previous post "Adverse Event of Special Interest (AESI), Standardized MedDRA Query (SMQs), Customer Queries (CQs), and SAS Programming"

AEs of Special Interest are usually the expected AEs.

An event can be an unexpected AE in the early development stage, but become the expected AE and AE of Special Interest in late stage. For example, during the TYSABRI® (natalizumab) (for multiple sclerosis) drug development, a rare brain infection—called progressive multifocal leukoencephalopathy (PML)— was unexpected in early stage, and then become an AE of Special Interest.

Grading the Severity of AEs and its Impact on AE Reporting

For all adverse events including serious adverse events in clinical trials, severity (or intensity) should be assessed and recorded. AE severity used to be called AE intensity. Nowadays, severity is more commonly used. The assessment of severity is based on the investigator’s clinical judgement, therefore, there are lot of subjective judgement in the AE severity assessment/reporting.

There seems to be three different grading scale in assessing/recording the severity:

Mild, Moderate, and Severe

This is commonly used in non-oncology studies. The definition of the mild, moderate, and severe may be different from one study protocol to another. The severity (intensity) of each AE including SAE recorded in the CRF should be assigned to one of the following categories:

• Mild: An event that is easily tolerated by the subject, causing minimal discomfort and not interfering with everyday activities.
• Moderate: An event that is sufficiently discomforting to interfere with normal everyday activities.
• Severe: An event that prevents normal everyday activities.

 or 

• Mild: awareness of sign or symptom, but easily tolerated
• Moderate: discomfort sufficient to cause interference with normal activities
• Severe: incapacitating, with inability to perform normal activities

CTCAE 

In oncology clinical trials, the AE severity is usually graded according to NCI’s AE Severity Grading Scale -  Common Terminology Criteria for Adverse Events (CTCAE). CTCAE can also be used to grade the AE for non-oncology studies, but generally not appropriate for studies using healthy volunteers.

• Grade 1 Mild; asymptomatic or mild symptoms; clinical or diagnostic observations only; no intervention indicated
• Grade 2 Moderate; minimal, local or noninvasive intervention indicated; limiting age-appropriate instrumental ADL
• Grade 3 Severe or medically significant but not immediately lifethreatening; hospitalization or prolongation of hospitalization indicated; disabling; limiting self care ADL
• Grade 4 Life-threatening consequences; urgent intervention indicated.
• Grade 5 Death related to AE.

Vaccine's Trials

In FDA’s guidance on vaccine trials “Toxicity GradingScale for Healthy Adult and Adolescent Volunteers Enrolled in PreventiveVaccine Clinical Trials”, the AE severity based on clinical abnormalities and laboratory abnormalities was graded as

• Mild (grade 1)
• Moderate (Grade 2)
• Severe (Grade 3)
• Potentially Life Threatening (Grade 4)

In statistical summaries, the grade 1 is counted as ‘mild’, the grade 2 as ‘moderate’, >= grade 3 will be counted as ‘severe’.  

During the course of an adverse event, the severity may change – which may have impact on how we report the adverse event.

In one of the previous posts ‘SAE Reconciliation and  Determining / recording the SAE Onset Date’, we discussed that an AE with the change in seriousness might need to be split into two events for recording: one non-serious AE with onset date of the first sign/symptom and one serious AE with onset date of the event meeting one of the SAE criteria. The similar issue arises when we try to record the AE with severity change.

The most common instruction for AE recording is that when there is severity change, a new AE should be recorded. Here are some example instructions:

Start Date
Record the date the adverse event started. The date should be recorded to the level of granularity known (e.g., year, year and month, complete date) and in the specified format. If a previously recorded AE worsens, a new record should be created with a new start date. There should be no AE start date prior to the date of the informed consent. Any AE that started prior to the informed consent date belongs instead in the medical history. If an item recorded on the medical history worsens during the study, the date of the worsening is entered as an AE with the start date as the date the condition worsened.

End Date
Record the date the adverse event stopped or worsened.  The date should be recorded to the level of granularity known (e.g., year, year and month, complete date) and in the specified format.  If an AE worsens, record an end date and create a new AE record with a new start date and severity. 

If the AE increases in severity per the DAIDS Grading Table, a new AE Log CRF should be completed to document this change in severity.

the eCRF Completion Guidelines for adverse events:  Enter a new event if action taken, seriousness, causality, severity (intensity), etc. changes over the course of an adverse event.  A timestamp for any changes in events can be seen in the data via event start/stop dates.

However, this way of recording the adverse events may result in splitting the single event into multiple adverse events and may result in over reporting in the number of adverse events.

Suppose the subject experienced a headache adverse event, the event started with mild intensity, then progressed to moderate, and then went back to the mild intensity. Should this headache be reported as three separate adverse events (two with mild severity and one with moderate severity)? or Should it be reported as single event with moderate severity?

This question was submitted to FDA and the FDA response (see the link below) suggested that this should be reported as one event (with the maximum severity)

AEReporting Question - Changes in Severity (03/08/2010)

The second question and answer explicitly stated:

Question 2:

[Redacted] is the sponsor of the study. We have been advised by our data coordinating center to record an AE that changes in severity as two AEs instead of 1 AE - starting a new AE each time the severity changes. This convention is different than that of our previous coordinating center and has caused us great concern.

Answer 2:

We have concerns that an approach to adverse event reporting as you described below (i.e., a change in severity of an adverse event necessitates a new adverse event report) may inaccurately reflect the adverse event profile for the product. Therefore, we strongly recommend that you contact the FDA review division regulating this clinical investigation for additional input on the most scientifically and medically sound approach to the adverse event reporting specifically for this trial.

I recently submitted this same question to FDA’s OC GCPQuestions and Answers and got the following response:

Question: 

We constantly run into the issue how to record the adverse event in the database in the situation there is a severity change or seriousness change during the course of the adverse event.
 A subject in clinical trial reported a mild headache. Two days later, the headache became moderate in severity. Then headache became mild in severity again.
 In this case, shall we record this as one headache event with moderate severity or record as three headache events (a new event is record whenever there is a severity change)?
 Similarly, a subject in clinical trial reported a non-serious adverse event. Several days later, subject needs to be hospitalized for this adverse event – now the event meets the seriousness criteria.
 In a situation of a non-serious adverse event becoming serious, shall we record it as a single AE with seriousness or shall we record as two separate AEs (one non-serious AE and one serious AE)?

OC-GCP Response:

Given your brief description that the subject's headache is ongoing, it would seem that this adverse event would best be reported as a single event with variable severity. However, the clinical judgment of the principal investigator (or, if the principal investigator is not a clinician, then a physician consultant to the research) would be helpful in clarifying the symptoms and hence the reporting of the adverse event(s). There are several cogent clinical scenarios the understanding of which would require more information than you have supplied. For example, the subject's symptomatology could represent an unremitting headache of several days duration or episodic headaches of finite duration with varying intensities or a symptom of another event altogether such as a change in blood pressure, etc. The same would apply for the hospitalization event.
 To best sort out the adverse event(s) itself and therefore the appropriate reporting, I would recommend a clinical assessment of the headache. In addition, the protocol may have detailed how adverse events should be reported. As well, the sponsor (I'm not sure of [Redacted] status in this trial, i.e., is/is not the sponsor) may have specifications for adverse event reporting that could guide you. If you still feel uncertain, I would strongly recommend contacting the FDA review division regulating this trial.
 Lastly, if it becomes apparent that this same "fact pattern" recurs, it may be advisable for the sponsor to clearly articulate standards for adverse event reporting such that there can be consistency in reporting of headaches.

From the statistical analysis standpoint, whether or not it is recorded as one event with maximum severity or multiple events with various seventies do not have impact on our calculation of the incidence of AEs. However, it will have great impact on the calculation of the number of AEs.

It is the common understanding that if an event recorded on the medical history worsens during the study or after the initiation of the study drug, a new AE should be recorded and the date of the worsening is entered as the new AE onset date

Clinical Trials Using Historical Control in Rare Disease Drug Development

While the randomized, control clinical trial has become and remains to be the golden standard in drug development, we also see the increased use of non-randomized, single-arm study where the effectiveness of the testing drug is compared to the historical control.

When a pivotal study is a single arm and has no concurrent control, the results from the study will need to be compared to the historical control or a common standard that has been accepted by the medical community or regulatory agencies. This seems to be more common in the oncology area and in rare disease areas.

Without any specific statistics, I can only say this is my impression that the historical control seems to be more accepted by the US FDA in its approvals in oncology and rare disease areas. Here are three examples of recent drug approvals based on historical control:

Venetoclax in Relapsed / Refractory Chronic Lymphocytic Leukemia (CLL)

The pivotal study is a single-arm study without concurrent control and the primary efficacy endpoint is objective response rate (ORR). The result is compared with the historical / standard rate of 40%.

• FDA approves new drug for chronic lymphocytic leukemia in patients with a specific chromosomal abnormality
• FDA NDA medical / statistical reviews
• Stilgenbauer et al (2016) Venetoclax in relapsed or refractory chronic lymphocytic leukaemia with 17p deletion: a multicentre, open-label, phase 2 study. Lancet Oncology

eteplirsen in Duchenne Muscular Dystrophy (DMD)

The original study was a randomized, double-blind, placebo control study with three arms (eteplirsen 30 mg/kg weekly; eteplirsen 50 mg/kg weekly, and placebo) – 4 subjects in each arm for a total 12 subjects. All subjects including placebo subjects were rolled over to an open-label extension study for long-term assessment.

The results from double-blind portion of the study did not provide the strong evidence for efficacy. The sponsor conducted a post-hoc comparison with a historical control.

FDA was not convinced with eteplirsen’s efficacy and conducted the advisory committee. In the end, the eteplirsen was approved as the first treatment in Duchenne Muscular Dystrophy with a lot of controversies. The comparison with historical control (while hotly debated) was a big part of the evidence contributing to the approval.

• FDA grants accelerated approval to first drug for Duchenne muscular dystrophy
• Mendell (2016) Longitudinal Effect of Eteplirsen versus Historical Control on Ambulation in Duchenne Muscular Dystrophy. ANN NEUROL
• FDA NDA Medical Review
• FDA NDA Statistical Review
• 2016 Meeting Materials, Peripheral and Central Nervous System Drugs Advisory Committee

Brineura for Batten Disease

The entire clinical program included: 

• A natural history study with 69 subjects (42 evaluable)
• A Phase 1/2 FIM single-arm study with 24 subjects (23 completed)
• A long-term follow-up study with 23 subjects

Natural history study was based on registry data; Provided the basis as the historical control group

Comparability between natural history study and phase 1/2 study were extensively debated during the review process.

FDA finally approved Brineura for Treating Batten disease in 2017.

• FDA approves first treatment for a form of Batten disease
• A Phase 1/2 Open-Label Dose-Escalation Study to Evaluate Safety, Tolerability, Pharmacokinetics, and Efficacy of Intracerebroventricular BMN 190 in Patients With Late-Infantile Neuronal Ceroid Lipofuscinosis (CLN2) Disease
• FDA NDA Summary Reviews
• FDA NDA Statistical Review

The use of historical control is not new. It was stated in the ICH guideline E10 “CHOICE OF CONTROL GROUP AND RELATED ISSUES IN CLINICAL TRIALS”

Historical control was again mentioned in FDA’s guidance for industry “Rare Diseases: Common Issues in Drug Development”. FDA encourages the natural history study to establish the historical control.

During the FDA advisory committee meeting, Dr Temple gave a presentation about "Historically Controlled Trials": see FDA's presentation slides (Dr Temple's presentation started from page 20).

In FDA's statistical review of eteplirsen in DMD, the following comments were made on the use of historical control: 

Historical Control Cohort
The comparison of eteplirsen with historical controls was not part of an adequate and wellcontrolled study. The applicant obtained historical data after observations were made for the eteplirsen patients. Historical data were obtained from 2 DMD patient registries (Italian DMD Registry and the Leuven Neuromuscular Reference Center – NMRC) for comparison to eteplirsen-treated patients
……
According to the ICH E10 guidance on Control Group and Related Issues in Clinical Trials, the major and well-recognized limitation of externally controlled (including historical control) trials is inability to control bias. The best group and control group can be dissimilar with respect to a wide range of observable and unobservable factors that could affect outcome. It may be possible to match the historical control group to the test group in observed factors but there is no assurance for any unobserved factors. “The lack of randomization and blinding, and the resultant problems with lack of assurance of comparability of test group and control group, make the possibility of substantial bias inherent in this design and impossible to quantitate.”
 Because of the serious concern about the inability to control bias, the use of the external control design is restricted only to unusual circumstances.

• ICH E10 states that “an externally controlled trial should generally be considered only when prior belief in the superiority of the test therapy to all available alternatives is so strong that alternative designs appear unacceptable…” However, such prior belief does not exist for eteplirsen.
• ICH E10 states that “use of external controls should be limited to cases in which the endpoints are objective…” however, performance on the 5-minute walk test can be influenced by motivation. Patients may not achieve maximal 6MWT due to concerns of falling or injury, or patients could try harder with encouragement and with the expectation that the drug might be effective.
• Pocock’s criteria for acceptability of a historical control group require that “the methods of treatment evaluation must be the same,” and “the previous study must have been performed in the same organization with largely the same clinical investigators.” This is especially important when assessing endpoints such as 6MWT, in contrast to hard endpoints such as mortality. For this NDA, these requirements are not met.

Moreover, the historical control group was identified post-hoc in this NDA, leading to potential selection bias that cannot be quantified. If a historical control is to be utilized, selection of the control group and matching on selection criteria should be prospectively planned without knowing the outcome of the drug group and control group.
 Based on ICH E10, “a consequence of the recognized inability to control bias is that the potential persuasiveness of findings from externally controlled trials depends on obtaining much more extreme levels of statistical significance and much larger estimated differences between treatments than would be considered necessary in concurrently controlled trials.” The success criteria for this historical control study were not discussed or pre-specified in the protocol.
 Given all these concerns, including issues of comparability of eteplirsen-treated patients and historical control cohort patients, the fact that 6MWT is not a “hard” efficacy endpoint, the potential of selection bias due to the post-hoc identification of the control cohort by the applicant, and all the known pitfalls with the use of historical controls, the comparison of the eteplirsen with historical control is not statistically interpretable. 

However, even though the statistical review on the use of historical control was very negative, the eteplirsen was still approved as the first drug treating the DMD and presumably the results from the comparison to historical control played the pivotal role in decision. 

In general, the use of historical control can be accepted in some situations especially in rare disease area where there is no approved drug available. Whenever the historical control is used, the following factors need to be considered:

• If the proposed historical control cohort is a priori or post hoc. It is encouraged to collect historical control information from natural history studies. 
• if the patient population from historical control is comparable
• If the outcome measurement is comparable
• if the outcome measurement is a hard endpoint (such as death) or soft endpoint (such as 6MWD)
• If the endpoint measure is easily affected by other factors
• if the endpoint is a soft endpoint (such as objective response rate ORR), whether or not any approach is implemented to avoid the bias (such as using central reader)

Generating graph / figure in publication quality

As I was recently preparing a poster for ATS Internal Conference, I was told that the plots I provided were not in high quality. When placing the plots on the poster, they became blurry. I realized that the issue was with the DPI. 

DPI is used to describe the resolution number of dots per inch in a digital print and the printing resolution of a hard copy print dot gain. High DPI = High Resolution.

The journal may have a requirement for the minimum resolution for the graphs and figures, for example, the PLOT One requires the resolution in the range of DPI 300-600. The Science magazine has the following requirement: 

Resolution. For manuscripts in the revision stage, adequate figure resolution is essential to a high-quality print and online rendering of your paper. Raster line art should have a minimum resolution of 600 dots per inch (dpi) and, preferably, should have a resolution of 1200 dpi. Grayscale and color artwork should have a minimum resolution of 400 dpi, and a higher resolution if possible.

Wiley had a paper discussing the challenges the authors might face for providing the high resolution figures. See the editorial: How to meet dots per inch requirements for images

I used SAS procedure sgplot to create the plots. The default DPI is 100, which is too low for publication or poster. Fortunately, there are easy ways to change the DPI for the output plots. Below are some programs for doing so: 

*default DPI=600; low resolution;
ods listing gpath='c:Temp\';
ods graphics on;
proc sgplot data=sashelp.stocks (where=(date >= "01jan2000"d
                                 and date <= "01jan2001"d
                                 and stock = "IBM"));
   title "Stock Volume vs. Close";
   vbar date / response=volume;
   vline date / response=close y2axis;
run;
ods graphics off;
ods listing close;

*set DPI=400;
ods listing gpath="c:\Temp\" dpi=400;
ods graphics on;
proc sgplot data=sashelp.stocks (where=(date >= "01jan2000"d
                                 and date <= "01jan2001"d
                                 and stock = "IBM"));
   title "Stock Volume vs. Close";
   vbar date / response=volume;
   vline date / response=close y2axis;
run;
ods graphics off;
ods listing close; 

*set DPI =400 and also use style=journal;
ods listing gpath="c:\Temp\" style=journal dpi=400;
ods graphics on;
proc sgplot data=sashelp.stocks (where=(date >= "01jan2000"d
                                 and date <= "01jan2001"d
                                 and stock = "IBM"));
   title "Stock Volume vs. Close";
   vbar date / response=volume;
   vline date / response=close y2axis;
run;
ods graphics off;

ods listing close;

When high DPI is chosen, the size of the file will increase. For the same plot, the file sizes for three plots (in png format) above are 26, 160, and 158 kb. 

The following program will service the same purpose, but use ods pdf commend. 

ods pdf file="c:\Temp\test.pdf";

proc sgplot data=sashelp.stocks (where=(date >= "01jan2000"d

                                 and date <= "01jan2001"d

                                 and stock = "IBM"));

   title "Stock Volume vs. Close";

   vbar date / response=volume;

   vline date / response=close y2axis;

run;

ods pdf close;

ods pdf file="c:\temp\test.pdf" dpi=600;

proc sgplot data=sashelp.stocks (where=(date >= "01jan2000"d

                                 and date <= "01jan2001"d

                                 and stock = "IBM"));

   title "Stock Volume vs. Close";

   vbar date / response=volume;

   vline date / response=close y2axis;

run;

ods pdf close;

ods pdf file="c:\Temp\test.pdf" style=journal dpi=600;

proc sgplot data=sashelp.stocks (where=(date >= "01jan2000"d

                                 and date <= "01jan2001"d

                                 and stock = "IBM"));

   title "Stock Volume vs. Close";

   vbar date / response=volume;

   vline date / response=close y2axis;

run;

ods pdf close;

The same issue with graph quality is also true when we use R. There is a RES = option to select the desired DPI. Please see the blog post by Daniel Hocking "High Resolution Figures in R".

Handling Randomization Errors in Clinical Trials with Stratified Randomization

Stratified randomization is very common in randomized, controlled clinical trials. The usage of stratified randomization has been discussed in previous posts. 

• Stratified randomization to achieve the balance of treatment assignment within each strata
• Restricted randomization, stratified randomization, and forced randomization
• Minimization Algorithm to Achieve Treatment Balance across Strata in Stratified Randomization

While stratified randomization has its benefits, it does not mean that more stratification factors are better. The more stratification factors we have, the more easily the randomization error of using a wrong stratum can occur. 

It becomes common to utilize the interactive response technology (IRT) system such as interactive response system (IVR) or interactive web response (IWR) systems for implementing the randomization and treatment assignments. The IRT system usually has to go through extensive quality control (QC) and user acceptance test (UAT) before implementation, therefore the randomization errors can be minimized. Compared to the manual randomization process, the randomization error rate is lower in studies with an IRT system for implementing the randomization. 

However, the use of the IRT system requires the investigational site staff (pharmacist, investigator, or study coordinator) to enter the stratification information at the time of randomization. The site staff can enter the incorrect stratification information into the IRT system, and the treatment assignment will then be pulled from the wrong stratum. The randomization error due to choosing a wrong stratum is probably the most common randomization error we see in clinical trials with stratified randomization. The more stratification factors we have, the more likely an incorrect stratum can be chosen. 

In addition to the number of stratification factors, ambiguous description/definition of the randomization stratum and lack of clarity about the source of measurement (for example, the local lab or central lab results for a lab-related stratification factor) can all contribute to choosing an incorrect stratum for randomization. 

For example, in a clinical trial in the neurology area, the sponsor plan to have patients stratified by their use of cholinesterase inhibitors, corticosteroids, immunosuppressant/immunomodulator. The following stratification factor is constructed.

• Regimen includes only cholinesterase inhibitors
• Regimen includes corticosteroid (CS) as the only
• immunosuppressant/immunomodulator, alone or in combination with other MG medications (e.g., a subject on prednisone plus a cholinesterase inhibitor would be in this stratum)

Without appropriate training, it is likely that the site staff will choose the wrong category for the randomization.

It is also common that the stratification factor is based on one of the laboratory measures. The original laboratory measure is a continuous result and it is then categorized for the stratification purpose. In this case, the protocol must be clear whether or not the stratification will be based on the lab results from the local lab or central lab because the results from local versus central labs can be different. 

When a wrong stratification stratum is chosen for the randomization (the randomization error occurs), the natural reaction is trying to fix it. However, with the IRT system, it is not easy to go back to the system to fix the randomization error. Actually it is strongly encouraged not to try to fix the issue. 

In a paper by Yelland et al "Applying the intention-to-treat principle in practice: Guidance on handling randomisation errors", the author concluded:

"...the safest option is to accept the randomisation errors that do occur and leave the initial randomisation records unchanged. This approach is consistent with the ITT principle, since it enables participants to be analysed as randomised, and avoids further problems that can arise when attempts are made to correct randomisation errors. A potential disadvantage of accepting randomisation errors is that imbalance could be introduced between the randomised groups in the number of participants or their baseline characteristics. However, any imbalance due to randomisation errors is expected to be minimal unless errors are common. Imbalance can be monitored by an independent data monitoring committee during the trial and investigated by the trial statistician at the analysis stage."

It is true that if randomization errors can skew the analyses especially when the occurrence of the randomization errors is not infrequent. In a paper by Ke et al "On Errors in Stratified Randomization", the impact of the randomization errors on treatment balance and properties of analysis approaches was evaluated. 

If there are a lot of randomization errors, the study's quality and integrity will be questioned. From the statistical analysis standpoint, the strict intention-to-treat analysis may not be appropriate. With a significant number of randomization errors with incorrect treatment assignments, we may need to analyze the data using 'as treated' instead of 'as randomized'. With a significant number of randomization errors due to incorrect selection of the randomization stratum, we may need to base the stratum information on the clinical database (assuming it is correctly recorded) instead of from the information used in the IRT system. 

When randomization errors are identified during a study, the root cause of the error should be investigated. Additional training may be needed to prevent the further occurrence of the randomization error. 

New FDA Guidance Documents for Drug Development in Neurological Conditions Aiming to Ease the Drug Approval Paths

This month, we saw FDA issued five guidance documents for drug development in five different neurological conditions/diseases (Alzheimer’s disease, DMD, ALS, Migraine, and Pediatric epilepsy). These newly issued guidance documents are intended to ease the drug approval requirements or offer the charities for the drug development pathway.

We think that this is a general trend in FDA and we expect that the similar guidance documents will be issued for other conditions/diseases aiming to ease the requirements for drug development – eventually speed up the drug development process, and the innovative drugs available to patients.

According to Statement from FDA Commissioner Scott Gottlieb, M.D. on advancing the development of novel treatments for neurological conditions; part of broader effort on modernizing FDA’s new drug review programs

“Today I’m pleased to issue five guidance documents that benefited from the streamlined approach of this pilot as part of a broader, programmatic focus on advancing treatments for neurological disorders that aren’t adequately addressed by available therapies. These guidance documents provide details on how researchers can best approach drug development for certain neurological conditions – Duchenne muscular dystrophy (DMD) and closely related conditions, migraine, epilepsy, AD and ALS. These guidance documents provide our current thinking and sound regulatory and scientific advice for product developers so that safe and effective treatments can ultimately be made available to patients. These documents are each a culmination of thoughtful scientific collaboration within the agency and incorporate important input from patients, researchers and advocates. We hope that providing up-to-date, clear information about our scientific expectations, such as clinical trial design and ways to measure effectiveness, will save companies time and resources and ultimately, bring effective new medicines to patients more efficiently.”

Below is a table to summarize the key points from these five guidance documents:

Indication	Guidance Title	Key Points
Alzheimer's disease	Early Alzheimer’s Disease: Developing Drugs for Treatment	No longer requiring co-primary efficacy endpoints to show the benefit in both cognitive and functional (or global) measures Staging the AZ as four different stages accepting different endpoints for different stages Allowing biomarker effects to be the primary endpoint in patients with Alzheimer pathology but no current symptoms
Duchenne muscular dystrophy (DMD) and related conditions	Duchenne Muscular Dystrophy and Related Dystrophinopathies: Developing Drugs for Treatment	Emphasizing the difficulties in designing trials of drugs for these conditions.  Efficacy endpoints, which basically leave it up to individual study sponsors to discuss with FDA staff the best approach on a case-by-case basis the DMD guideline did not do, is open a path for approval based solely on biomarker effects such dystrophin levels in muscle, although, effects on objective measures such as respiratory and cardiac muscle function can be used to support approval.
Amyotrophic lateral sclerosis (ALS)	Amyotrophic Lateral Sclerosis: Developing Drugs for Treatment	Offering more clarity Efficacy must be demonstrated at "clinically meaningful" levels for symptoms, function, or survival -- period
Migraine	Migraine: Developing Drugs for Acute Treatment	Sponsors would no longer be required to conduct trials addressing four different classes of symptoms: pain, nausea, photophobia, and phonophobia. Trials will only need two primary endpoints: pain reduction and effects on individual patients' "most bothersome symptom."
Pediatric epilepsy	Drugs for Treatment of Partial Onset Seizures: Full Extrapolation of Efficacy from Adults to Pediatric Patients 4 Years of Age and Older	For drugs intended for children age 4 and older with partial onset seizures, the FDA will no longer require that efficacy trials be conducted in children. The agency will now consider efficacy data from adult patients to be sufficient for pediatric approval.

Weighted Bonferroni Method (or partition of alpha) in Clinical Trials with Multiple Endpoints

In a previous post, the terms of ‘multiple endpoints’ and ‘co-primary endpoints’ were discussed. If a study contains two co-primary efficacy endpoints, study is claimed to be successful if both endpoints have statistical significance at alpha=0.05 (no adjustment for multiplicity is necessary). If a study contains multiple (two) primary efficacy endpoints, the study is claimed to be successful if either endpoint is statistically significant. However, in later situation, the adjustment for multiplicity is necessary to maintain the overall alpha at 0.05. In other words, for hypothesis test for each individual endpoint, the significant level alpha is less than 0.05.

The most simple and straightforward approach is to apply the Bonferroni correction. The Bonferroni correction compensates for the increase in number of hypothesis tests. each individual hypothesis is tested at a significance level of alpha/m, where alpha is the desired overall alpha level (usually 0.05) and m is the number of hypotheses. If there are two hypothesis tests (m=2), each individual hypothesis will be tested at alpha=0.025.

In FDA guidance 'Multiple Endpoints in Clinical Trials', the Bonferroni Method was described as the following:

The Bonferroni method is a single-step procedure that is commonly used, perhaps because of its simplicity and broad applicability. It is a conservative test and a finding that survives a Bonferroni adjustment is a credible trial outcome. The drug is considered to have shown effects for each endpoint that succeeds on this test. The Holm and Hochberg methods are more powerful than the Bonferroni method for primary endpoints and are therefore preferable in many cases. However, for reasons detailed in sections IV.C.2-3, sponsors may still wish to use the Bonferroni method for primary endpoints in order to maximize power for secondary endpoints or because the assumptions of the Hochberg method are not justified. The most common form of the Bonferroni method divides the available total alpha (typically 0.05) equally among the chosen endpoints. The method then concludes that a treatment effect is significant at the alpha level for each one of the m endpoints for which the endpoint’s p-value is less than α /m. Thus, with two endpoints, the critical alpha for each endpoint is 0.025, with four endpoints it is 0.0125, and so on. Therefore, if a trial with four endpoints produces two-sided p values of 0.012, 0.026, 0.016, and 0.055 for its four primary endpoints, the Bonferroni method would compare each of these p-values to the divided alpha of 0.0125. The method would conclude that there was a significant treatment effect at level 0.05 for only the first endpoint, because only the first endpoint has a p-value of less than 0.0125 (0.012). If two of the p-values were below 0.0125, then the drug would be considered to have demonstrated effectiveness on both of the specific health effects evaluated by the two endpoints. The Bonferroni method tends to be conservative for the study overall Type I error rate if the endpoints are positively correlated, especially when there are a large number of positively correlated endpoints. Consider a case in which all of three endpoints give nominal p-values between 0.025 and 0.05, i.e., all ‘significant’ at the 0.05 level but none significant under the Bonferroni method. Such an outcome seems intuitively to show effectiveness on all three endpoints, but each would fail the Bonferroni test. When there are more than two endpoints with, for example, correlation of 0.6 to 0.8 between them, the true family-wise Type I error rate may decrease from 0.05 to approximately 0.04 to 0.03, respectively, with negative impact on the Type II error rate. Because it is difficult to know the true correlation structure among different endpoints (not simply the observed correlations within the dataset of the particular study), it is generally not possible to statistically adjust (relax) the Type I error rate for such correlations. When a multiple-arm study design is used (e.g., with several dose-level groups), there are methods that take into account the correlation arising from comparing each treatment group to a common control group.

The guidance also discussed the weighted Bonferroni approach:

The Bonferroni test can also be performed with different weights assigned to endpoints, with the sum of the relative weights equal to 1.0 (e.g., 0.4, 0.1, 0.3, and 0.2, for four endpoints). These weights are prespecified in the design of the trial, taking into consideration the clinical importance of the endpoints, the likelihood of success, or other factors. There are two ways to perform the weighted Bonferroni test:  

• The unequally weighted Bonferroni method is often applied by dividing the overall alpha (e.g., 0.05) into unequal portions, prospectively assigning a specific amount of alpha to each endpoint by multiplying the overall alpha by the assigned weight factor. The sum of the endpoint-specific alphas will always be the overall alpha, and each endpoint’s calculated p-value is compared to the assigned endpoint-specific alpha.
• An alternative approach is to adjust the raw calculated p-value for each endpoint by the fractional weight assigned to it (i.e., divide each raw p-value by the endpoint’s weight factor), and then compare the adjusted p-values to the overall alpha of 0.05.

These two approaches are equivalent

The guidance mentioned that reason for using the weighted Bonferroni test are:

• Clinical importance of the endpoints
• The likelihood of success
• Other factors

Other factors could include:

• With two primary efficacy endpoints, the expectation for regulatory approval for one endpoint is greater than another
• Sample size calculation indicates that the sample size that is sufficient for primary efficacy endpoint #1 is overestimated for the primary efficacy endpoint #2 

With the weighted Bonferroni correction, the weights are subjective and are essentially arbitrarily selected which results in the partition of unequal significant levels (alphas) for different endpoints.

There are a lot of applications of Bonferroni and weighted Bonferroni in practice. Here are some examples: 

In the publication Antonia 2017 "Durvalumab after Chemoradiotherapy in Stage III Non–Small-Cell Lung Cancer", two coprimary end points were used in the study

The study was to be considered positive if either of the two coprimary end points, progression free or overall survival, was significantly longer with durvalumab than with placebo. Approximately 702 patients were needed for 2:1 randomization to obtain 458 progression-free survival events for the primary analysis of progressionfree survival and 491 overall survival events for the primary analysis of overall survival. It was estimated that the study would have a 95% or greater power to detect a hazard ratio for disease progression or death of 0.67 and a 85% or greater power to detect a hazard ratio for death of 0.73, on the basis of a log-rank test with a two-sided significance level of 2.5% for each coprimary end point.

However, in the original study protocol, the weighted Bonferroni method was used and unequal alpha levels were assigned to OS and PFS.  

The two co-primary endpoints of this study are OS and PFS. The control for type-I error, a significance level of 4.5% will be used for analysis of OS and a significance level of 0.5% will be used for analysis of PFS. The study will be considered positive (a success) if either the PFS analysis results and/or the OS analysis results are statistically significant.

Here, a weight of 0.9 (resulting in an alpha 0.9 x 0.05 = 0.045) was given to OS and a weight of 0.1 (resulting in an alpha 0.1 x 0.05 = 0.005) was given to PFS.

In COMPASS-2 Study (Bosentan added to sildenafil therapy in patients with pulmonary arterial hypertension), the original protocol contained two primary efficacy endpoints and weighted Bonferroni method (even though it was not explicitly mentioned in publication) was used for multipolicy adjustment. A weight of 0.8 (resulting in an alpha 0.8 x 0.05 = 0.04) was given to time to first mortality/morbidity event and a weight of 0.2 (resulting in an alpha 0.2 x 0.05 = 0.01) was given to the change from baseline to Week 16 in 6MWD.

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 PAHs, 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 change 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).

According to FDA’s briefing book on” Ciprofloxacin Dry Powder for Inhalation (DPI)

Meeting of the Antimicrobial Drugs Advisory Committee (AMDAC) “, the sponsor (Bayer) conducted two pivotal studies: RESPIRE 1 and RESPIRE 2. Each study contained two hypotheses. Interestingly, for multiplicity adjustment, the Bonferroni method was used for RESPIRE 1 study and the weighted Bonferroni method for RESPIRE 2 study. We can only guess why weights of 0.02 and 0.98 (resulting in a partition of alpha of 0.001 and 0.049) was chosen in RESPIRE 2 study

RESPIRE 1 Study:

• 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:

• 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)