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Biostatistics in cancer RCTs
1. Biostatistics in Cancer Clinical Trials
Presented at the “Recent Trends in Bio-Medical Biostatistics”,
Gujarat University, Ahmedabad on 24.02.2007
Dr. Bhaswat S. Chakraborty
VP, R&D, Cadila Pharmaceuticals Ltd.
2. Contents
Research and Regulations of Cancer Trials
Pivotal Cancer Trials (Phase III)
Efficacy end points
Merits and demerits
Optimum Study Designs
Superiority
Non-Inferiority and other designs
Sample Size Considerations
Scientific questions
Basics of sample size calculation
Statistical Plan for a Cancer RCT
Statistical Analysis of Cancer Data
Tumor Data Analysis – an Example
Conclusion
7. Cancer Research Today
Research is conducted mainly on
New Drugs
New Combinations
Radiotherapy
Surgery
In the West, research is usually done by large co-operative groups, in
addition to those mentioned for India
In India
Large Pharmaceuticals
Co-operative Groups, e.g., ICON (Indian Co-operative Oncology Network)
Regional Cancer Centres & Govt. sponsored studies
Academia
8. What does FDA Look for?
FDA approves a drug application based on
Substantial evidence of efficacy & safety from
“adequate and well-controlled investigations”
A valid comparison to a control
Quantitative assessment of the drug‟s effect
(21 CFR 314.126.)
The design of cancer trials intended to support
drug approval is very important
9. Study Design: Approaches
Randomised Controlled Trials (RCT) most preferred
approach
Demonstrating superiority of the new therapy
Other approaches
Single arm studies (e.g., Phase II)
e.g., when many complete responses were observed or
when toxicity was minimal or modest
Equivalence Trials
No Treatment or Placebo Control Studies
Isolating Drug Effect in Combinations
Studies for Radio- and Chemotherapy Protectants
10. Randomized Clinical Trials
Gold standard in Phase III
Single centre CT
Primary and secondary indications
Safety profile in patients
Pharmacological / toxicological characteristics
Multi-centre CT
Confirmation of the above
Effect size
Site, care and demographic differences
Epidemiological determination
Complexity
Far superior to meta-analyzed determination of effect
11. Non-Inferiority Trials
New drug not less effective by a predefined
amount, the noninferiority (NI) margin
NI margin cannot be larger than the effect of the
control drug in the new study
If the new drug is inferior by more than the NI
margin, it would have no effect at all
NI margin is some fraction of (e.g., 50 percent) of
the control drug effect
12. Placebo Control Equality Trials
No anticancer drug treatment in the control arm is
unethical
Sometimes acceptable
E.g., in early stage cancer when standard practice is to give
no treatment
Add-on design (also for adjuvants)
all patients receive standard treatment plus either no
additional treatment or the experimental drug
Placebos preferred to no-treatment controls because they
permit blinding
Unless very low toxicity, blinding may not be feasible
because of a relatively high rate of recognizable toxicities
13. Drug or Therapy Combinations
Use the add-on design
Standard + Placebo
Standard + Drug X
Effects seen in early phases of development
Establish the contribution of a drug to a standard
regimen
Particularly if the combination is more effective
than any of the individual components
14. What to Measure?
Time to event end points
Survival
Disease free survival
Progress (of disease) free survival
Objective response rates
Complete
Partial
Stable disease
Progressive disease
Symptom end points
Palliation
QoL
15. Cancer Trials – End Points
Endpoint Evidence Assessment Some Advantages Some Disadvantages
Survival Clinical benefit RCT needed Direct measure of Requires larger and
Blinding not benefit longer studies
essential Easily Potentially affected by
measured crossover therapy
Precisely Does not capture
measured symptom benefit
Includes noncancer
deaths
Disease-Free Surrogate for RCT needed Considered to Not a validated
Survival accelerated Blinding be clinical benefit survival surrogate in most
(DFS) approval or preferred by some settings
regular Needs fewer Subject to assessment
approval* patients and bias
shorter studies Various definitions
than survival exist
16. Cancer Trials – End Points
Endpoint Evidence Assessment Some Advantages Some Disadvantages
Objective Surrogate for Single-arm or Can be assessed Not a direct measure of
Response accelerated randomized in single-arm benefit
Rate (ORR) approval or studies can be studies Usually reflects drug
regular used activity in a minority of
approval* Blinding patients
preferred in Data are moderately
comparative complex compared to
studies survival
Complete Surrogate for Single-arm or Durable CRs Few drugs produce high
Response accelerated randomized represent obvious rates of CR
(CR) approval or studies can be benefit in some Data are moderately
regular used settings (see text) complex compared to
approval* Blinding Can be assessed survival
preferred in in single-arm
comparative studies
studies
18. Phase III Cancer Trials
New Drug (or Regimen) is
Compared with a Standard
90
80 New
70 Standard
60
50
40
30
20
10
0
Superiority Trials Survival DFS QoL
19. Phase III Cancer Trials
40
35 New
30 Standard
25
20
15
10
5
0
Survival DFS QoL
Non-Inferiority or Equivalence Trials
20. Understanding Basics
μ0 and μA
Means under Null & Alternate Hypotheses
σ02 and σA2
Variances under Null & Alternate Hypotheses (may be the same)
N0 and NA
Sample Sizes in two groups (may be the same)
H0: Null Hypothesis
μ0 – μA = 0
HA: Alternate Hypothesis
μ0 – μA = δ
Type I Error (α): False +ve
Probability of rejecting a true H0
Type II Error (β): False –ve
Probability of rejecting a true HA
Power (1-β): True +ve
Probability of accepting a true HA
21. Basics of Sample Size Calculation
Answer the scientific questions for the Trial size
Understand the distribution and variability of the data
Construct correct Null and Alternate hypotheses
From the hypotheses derive formula for sample size
Also make sure that this size trial has adequate power
to establish a true alternate
22. Five Key Questions
1. What is the main purpose of the trial?
2. What is the principal measure of patient outcome?
3. How will the data be analysed to detect a treatment
difference?
4. What type of results does one anticipate with standard
treatment?
5. How small a treatment difference is it important to detect
and with what degree of certainty?
Answers to all of the five questions above enable us to
calculate the sample size and analyze the data with most
appropriate test of hypothesis.
Pocock SJ: Clinical Trials: A Practical Approach Chichester: Wiley; 1983
23. Start
Planning Reliable or historical
data available? No
Yes Use conventional
methods for analysis
Use bootstrap simulation for
sample size
Normally distributed
continuous data? Summary
Yes
measure: mean & mean
μT – μC difference
∆normal = Use parametric methods of
σ analysis, two sample ‘t’ or
ANOVA
Effect Size
No
2 [Z1-α/2 + Z1-β/2]2
Use non-parametric methods
Nnormal =
∆2normal of analysis, Mann-Whitney U
or Proportional Odds Model
Sample Size
28. Sample and Power for Simulated Tumor
Data
Expected Relative Risk
1
0.8
0.6 86
0.4 64
50
0.2
110
0
0.3 0.4 0.5 0.6 0.7 0.8
Relative risk
29. Statistical Plan
Primary outcome considerations
Study Design
Sample size calculation
Randomization
Statistical consideration in Inclusion/Exclusion criteria
(Homogeneity within centre and strata)
Accrual of patients
Cleaning of data
Interim Analysis
Go/No go criteria
α Considerations
Final analysis
Final conclusions
30. Accrual of Patients
Study of the statistical trends in accrual patterns
Seasonal
Planned approaches
Reasons for drop outs and loss to follow up
Motivational factors
Monitoring of recruitment progress and strategies
Frequency
Parameters
Duration
Understanding natural history and non-cancer, non-intervention deaths
Changes in accrual after Interim Analysis
31. Randomisation
Generation of randomisation scheme according to
Centre
Block
Strata
Patient
Investigational Product to be given
Measures of ensuring non-bias
Allocations
What should go on the labels
Primary, secondary, tertiary packaging
32. Blinding
Often difficult in oncology trials
Test and control are of different characteristics
Different routes of administration
Different schedules
New low toxicity oral treatments are relatively easy to
blind
In other cases the end-point evaluating investigator
must be different from the one administering the drugs
33. Data Capture
Manual or Electronic
CRF is the main source of raw data capture
Data must be quality assured
Integrity, accountability, traceability
Data must be validated
All production and/or quality system software, purchased or
developed in-house
Should document
Intended use, and information against which testing results and other
evidence can be compared
To show that the software is validated for its intended use
34. Data Cleaning & Locking
Data are cleaned based on a good plan for interim or final analysis
E.g.,
Hundred percent data are made quality checked and assured
Eligibility criteria for data selection
Correction and editing
Double data entry or other methods of data integrity
Data will be locked after cleaning the data and resolving all the
queries
SOP for data locking
No change after locking
Only locked data are used as input into data analysis program
35. Interim Analysis of Data
0.05
0.045
0.04
0.035
0.03
0.025
Nominal p
0.02
0.015
0.01
0.005
0
1 2 3 4
Looks
36. Interim Analysis of Data
2 Look
3s Lo
How many times
NominalPvue 0.3 0.5
NominalPvue 0.3 0.5
can you look into
the data?
o p o c o c k
o o b + fle
o fle + h a r + o b
0. 0.1
0. 0.1
1 2 1 2 3
L o o k L o o k
4 Look
5s Lo
NominalPvue 0.3 0.5
NominalPvue 0.3 0.5
Type 1 error at kth
test is NOT the
same as the
nominal p value
0. 0.1
for the kth test 1 2 3
L o o k
0. 0.1
4 1 2 3 4
L o o k
5
37. Considerations for IA
Stopping rules for significant efficacy
Stopping rules for futility
Measures taken to minimize bias
A procedure/method for preparation of data for analysis
Data has to be centrally pooled, cleaned and locked
Data analysis - blinded or unblinded?
To whom the interim results will be submitted?
DSMB
Expert Steering Group
What is the scope of recommendations from IA results?
Safety? Efficacy? Both? Futility? Sample size readjustment
for borderline results?
38. Final Analysis and Conclusion
Clinically meaningful margins must be well defined in Control trials
prospectively
Superiority and non-inferiority margins must not be confused
Two or one-sidedness of α should also be prospectively defined
Power must be adequate
Variance must be analysed using the right model
Strategy for dealing with multiple end points must be prespecified
Too many end points ot tests will increase the false positive (α) error
Sometimes (e.g., in equality trials) statistically significant results may not
be medically significant
Data censoring or skewed data
E.g., time to event data
39. Intent-to-Treat Principle
All randomized patients
Exclusions on prespecified baseline criteria permissible
also known as Modified Intent-to-Treat
Confusion regarding intent-to-treat population: define and agree
upon in advance based upon desired indication
Advantages:
Comparison protected by randomization
Guards against bias when dropping out is realted to outcome
Can be interpreted as comparison of two strategies
Failure to take drug is informative
Refects the way treatments will perform in population
Concerns:
“Difference detecting ability”
40. Per Protocol Analyses
Focuses on the outcome data
Addresses what happens to patients who remain on
therapy
Typically excludes patients with missing or
problematic data
Statistical concerns:
Selection bias
Bias difficult to assess
41. Intent to Treat & Per Protocol Analyses
Both types of analyses are important for approval
Results should be logically consistent
Design protocol and monitor trial to minimize
exclusions
Substantial missing data and poor drug compliance
weaken trial‟s ability to demonstrate efficacy
42. Missing Data
Protocol should specify preferred method for
dealing with missing primary endpoint
ITT
e.g., treat missing as failures
e.g., assign outcome based on blinded case-by-case
review
Per Protocol
e.g., exclusion of patients with missing endpoint
43. Data Safety and Monitoring Board (DSMB)
All trials may not need a DSMB
DSMB Membership
Medical Oncologist, Biostatistician and Ethicist
Statistical expertise is a key constituent of a DSMB
Three Critical Issues
Risk to participants
Practicality of periodic review of a trial
Scientific validity of the trial
46. Control Group
Simulated Tumor Data: An Example
70
Survival Time (Days)
60
50
40
30
20
10
0
1 4 7 10 13 16 19 22 25 28 31 34 37 40 43 46
Patient No
Experimental Group
250
Survival Time (days)
200
150
100
50
0
1 3 5 7 9 11 13 15 17 19 21 23 25 27 29 31 33 35 37
Patient No
47. Descriptive Statistics
± Standard deviation
120
100
80
time
60 Variable: time
grouped by: group
40 95%
N Mean Conf. (±) Std.Error Std.Dev.
20
1 48 15.77083333 4.241619672 2.108375644 14.60725495
0 2 38 47.73684211 19.66266124 9.704135603 59.8203094
1 2
Entire sample 86 29.89534884 9.420677178 4.738064537 43.93900293
group
48. Log-rank Test (Cox-Mantel)
Events Events
Kaplan Meier observed expected
1 29 21.09256306
2 18 25.90743694
Degrees of
1.2 Chi-square Freedom P
1 6.369814034 1 0.011607777
0.8
Probability
Censored
0.6 1
2
0.4
0.2
0
0 50 100 150 200 250
tim e
49. Cox Regression
at Mean
1.2
1
0.8
Probability 0.6
0.4
0.2
0
0 50 100 150 200 250
tim e
95% Hazard =
Coefficient Conf. (±) Std.Error P Exp(Coef.)
-0.823394288 0.667410889 0.340517244 0.015603315 0.438939237
50. Conclusion of Tumor Data
Kaplan Meier
Two survival patterns are different with a median of 12 and 70 days
for the Control and Experimental Groups
Log-Rank Test
The p-value of 0.0116 indicates significantly higher survival
experience of the experimental group
Cox Regression
Hazard of death for the Experimental group is estimated to be about
44% that of the Control group
The log hazard coefficient is – 0.8234 (hence, e-0.8234=0.4389,
which gives us the estimated unadjusted Experimental hazard
ratio). It means that the expected log hazard for the Experimental
group is .8234 lower than it is for the Control group
Difference in survival time in Experimental & Control groups is
highly significant (p=0.0156)
51. Conclusions
Clinical testing of new Oncology products is very sophisticated
and complex
A Statistician‟s role in Cancer trials is invaluable
Statistical considerations must be thoroughly given attention and
built in while planning the study design and calculating the
sample size
Cancer clinical data is very complex (censored, skewed, often
fraught with missing data point), therefore, proper
hypothesization and statistical treatment of data are required
Prospective RCTs are usually the preferred approach for
evaluation of new therapies
52. Conclusions
Survival as primary end point is preferred by regulatory agencies
Randomisation and blinding offer a robust way to remove bias in end-point
estimations
Data must be accurately captured without any bias and analysed by
prospectively described methods
Interim analysis should carefully plan „ spending’ function
Final analysis should be done carefully, independently and meaningfully
(medical as well as scientific)
Choose clinically relevant delta
Design, conduct, and monitor trials to minimize missing data and poor compliance
to drug
Analysis
Both intent-to-treat and per protocol analyses should be conducted
Sensitivity analyses
There are many oustanding statistical issues in Cancer trials that need no be
discussed and solved
53. Acknowledgements
Dr. Nikunj Patel
Dr. Sumit Goyal
Dr. Manish Harsh
Dr. Nilesh Patel
Ms. Darshini Shah
Thank You Very Much