adverse events temporally associated with infusion

In biological field, it is pretty common to collect and analyze the adverse events that are temporally associated with an infusion. For example, this is required in a recent FDA guidance about IGIV (http://www.fda.gov/cber/gdlns/igivimmuno.pdf). The guidance stated “Your protocol should define criteria for establishing an AE as an infusional AE (i.e., an AE temporally associated with an infusion). We recommend you list AEs individually by body system with subject identification numbers and report the overall incidences of all AEs that occur during or within: (a) 1 hour, (b) 24 hours, and (c) 72 hours following an infusion of test product, regardless of other factors that may impact a possible causal association with product administration.”

While this is understandable, we need to be clear about the exact time frame for collecting these AEs when coming to the programming. I had a couple of studies where the definition (therefore the calculation) of the infusion related adverse events are defined differently “Infusion related adverse events are defined as any event that occurs within 1 hour, 24 hours, or 72 hours of initiation of the study drug infusion.” While this is not wrong, the time frame is shorter for counting the infusion related adverse events.

To be crystal clear about the time period where the infusion related AEs are collected, the following sentence seems to be better.

“The incidence of adverse events considered potentially related to Flebogamma 5% DIF during or within 72 hour after completing an infusion…” (refer to http://www.ncbi.nlm.nih.gov/pubmed/17909953?ordinalpos=1&itool=EntrezSystem2.PEntrez.Pubmed.Pubmed_ResultsPanel.Pubmed_RVDocSum”

Quantile regression

Typically, the physicians will listen to statisticians for statistical analysis approaches. In some cases, the physicians can be very smart and knowledgable in statistics. In a recent discussion about exploring the correlation between change in INCAT (a scale for measuring the functional disability) and change in amplitude (a neurophysiology measure), I performed the simple correlation and calculated the Pearson's correlation coefficient. The scatter plot with fitted linear regression line were shown on the right side figure. One of the investigators pointed out that the correlation line drawn in the figure is not the maximum we can get out of it. He think that a curvilinear fitting may be better.

Through his reminder, I refit the data using spline fitting by adding quadratic term and/or cubic terms to the linear regression, the result is no better. I also learned the new regression approach, quantile regression. It turned out that the quantile regression is similar to the linear regression, but is trying to minimize the distance between the observed value and the quantile (median, 75th quantile,...) instead of minimizing the distance between the observed value and the mean. The SAS actually provided an experimental version of Quanreg procedure. The procedure can be downloaded from SAS website for free. http://support.sas.com/rnd/app/da/quantreg.html.

http://www2.sas.com/proceedings/sugi30/213-30.pdf

For my question, the quantile regression is not better than the linear regression or simply correlation.

Some words about adaptive design

Four rules to adapt by:

• Allocation rule: how subjects will be allocated to the avaialble arms
• Sampling rule: how many subjects will be sampled in subsequent stages
• Stopping rule: when to drop an arm or stop the trial (for efficacy, harm or futility)
• Decision rule: the final decision and interim decisions pertaining to design changes not covered in the previous three rules. Examples of the modifications that can result from these decision-making rules include modifying the sample size, dropping a treatment arm, stopping a study early for success or failure, combining phases, and/or adaptive randomization

Adaptive trials can involve any one of these rules, or a combination of them

Top three misconceptions of adaptive trials:

• There are certain areas of confirmatory clinical research where adaptive designs are more applicable and other areas where adaptive designs are less or not applicable
• Adaptive trial designs are characterized by unmanageable complexity and less careful planning
• Adaptive designs require smaller sample sizes than traditional designs

Human beings lean toward wishful thinking. On average, drug effects are overestimated and the variability of drug effects is underestimated. As yet, trials have either been unknowingly underpowered or intentionally overpowered. In the latter case, an adaptive design is more or less unnecessary (aside from the questionable ethics of overpowered trials). The unknowingly underpowered trials, however, is where adaptive designs come into plan. By using an adaptive design, a potentially underpowered trial can be rescued. Overall, adaptive designs make better use of the patient as a resource. Trials no long need to be overpowered, and the number of underpowered trials is rescued.

The heavy burden of the modern clinical trial protocols

A recent article by Mr Getz in Applied Clinical Trials elaborated the heavy burden of protocol design in modern clinical trials. The clinical trial design become more and more complicated, requiring more study procedures, collecting more items. More complex and demanding protocols are hurting clinical trial performance and success.

I absolutely agree with his assessment. I can even add that the protocol design may also require more blood draws from the participants for hematology, chemistry, viral testing, biomarkers, pharmacokinetics, pharmacogenetics,… In some studies, patients may be exposed to more radio material exposures than ever. I even heard that a sponsor provided a comprehensive protocol with adaptive study design with many pages of appendices to describe how Bayesian algorithms are applied. We can imagine the reaction from investigator, CRA, even CRO statisticians. I don’t know how the investigator can understand these Bayesian algorithms. One question that needs to be answered is the target of the study protocol: is it for investigators? For regulatory authorities? For IRBs? For CRAs? Or for all of them?

Everything has a balance. Eventually we will get to a point that a too complex and too demanding protocol may actual hurt the study from every aspect in terms of the cost, resource, patient enrollment, data quality, generalization of the study results,…

Who to blame? I can think of the followings:
Regulatory requirement is getting tighter and tighter.
The sponsor is getting more conservative
The sponsor is trying to collect as much information as they can with no distinguishing of the items that are really necessary and the items that is merely nice to have.
Key opinion leaders are often asking for additional items to be added to the protocol for their own interest.

Communication with non-statisticians

My fellow colleague expressed his frustration about exlaining a statistical concept to our clinical operation colleagues. I fully undertood his feelings. Sometimes, it is not easy to communicate with non-statisticians. The problem could be on both sides: stastician did not use the plain English or non-statisticians lacked the understanding of very basic statistics.

Considering my medical background, I feel a little lucky when communicating with physicians or non-statisticians. Perhaps also because of my teaching experience, I knew how to explain the complicated statistical issues in plain language to the non-statisticians. So I have one area I am proud of myself.

Below I picked up an example to demonstrate how differently the statistical terms can be explained.

Regarding three types of missing data mechnisms, here are the definition from a recent article in Drug Information Journal:

• Data are considered missing completely at random (MCAR) if, conditional upon the independent variables in the analytic model, the missingness does not depend on either the observed or unobserved outcomes of the variable being analyzed (Y)
• Data are missing at random (MAR) if, conditional upon the independent variables in the analytic model, the missingness depends on the observed outcomes of the variable being analyzed (Yobs) but does not depend on the unobserved outcomes of the variable being analyzed (Ymiss).
• Data are missing not at random (MNAR) if, conditional upon the independent variables in the analytic model, the missingness depends on the unobserved outcomes of the variable being analyzed.

Now, for the same concept, the following definitions seem to be better understandable.

• MCAR (data are missing completely at random): A "missing" value does not depend on the variable itself or on the values of other variables in the database.
• MAR (data are missing at random): The probability of missing data on any variable is not related to its particular value. The pattern of missing data is traceable or predictable from other variables in the database.
• NMAR (not missing at random): Missing data are not random and depend on the values that are missing.

Rule of three

Rule of three states that consider a Bernoulli random variable with unknown probability p, if in n independent trials no events occur, a quick-and-ready approximation to the upper 95% confidence bound for p is 3/n.
This rule has particularly been used in pre-licensure clinical trials where the adverse event rate is very rare. Sample sizes of pivotal trials for licensure are set for an efficacy endpoint, and vary according to the indication. Therefore, pivotal confirmatory studies provide adequate denominators for determining adverse events that occur at a frequency higher than or similar to the clinical efficacy outcome. However, sample sizes are not sufficient for detecting the rare events. Only reliable post-marketing surveillance systems will allow detection of a rare adverse event or a small increase in adverse event rate.
Rule of three provides a quick calculation of the upper confidence interval of the observed rate (observed rate is zero when there is no event occurred). It is based on the estimated upper limit of the 95% confidence interval when this particular event has not occurred during a clinical trial or during the clinical development program. As an example in vaccine development program, if no event has been observed with a sample size of 100, the upper limit of the 95% CI of the rate of this event is 3%. A sample size in the range of 10 000 subjects can be considered adequate for establishing the protective efficacy of a new vaccine. If no event of any particular sort has been observed during a pre-licensure clinical program involving 10 000 individuals, it can be estimated that this event rate has an upper limit of 3 per 10 000. Rarer adverse events, those occurring at a lower frequency than the vaccine-targeted disease, or an increase in rare adverse events, are unlikely to be detected before licensure their assessment must rely on post-marketing studies (phase IV).
However, if the rare event does occur during the clinical trial (the event rate is not zero), the rule of three should not be used. Instead, the confidence interval should be calculated according to exact or permutation approach (not the formula that is based on the normal approximation).

Also, we should not attempt to calculate the sample size based on the rule of three. The sample size should still be based on the efficacy endpoint instead of the comparison of the rare events – otherwise, the sample size could be huge.

References:
1. Ernst Eypasch et al. Probability of adverse events that have not yet occurred: a statistical reminder. BMJ 1995
2. Steve Simon's web blog. Stistical confidence interval with zero event

Comparing treatment difference in slopes

In regulatory setting, can we showing the treatment difference by comparing the slopes between two treatment groups?
In a COPD study (e.g., a two arm, parallel group with primary efficacy variable measured at baseline and every 6 months thereafter), one can fit the random coefficient model and compare the treatment difference between two slopes. Also we can compare the treatment difference in terms of change from baseline to the endpoint (the last measure).
To test the difference in slopes, we would need to test whether or not the treatment*time interaction term is statistically significant. The assumption is that at the beginning of the trial, the intercept for both groups are the same - both groups started at the time level. Then if the treatment can slow the disease progression, the treatment group should show a smaller slope comparing with the placebo group.
If all patients are followed up to the end of the study, if the slopes are different, the endpoint (change from baseline) analysis should also be statistically different. However, with a smaller sample size, the results could be inconsistent by using slope comparison approach vs. endpoint analysis approach. For a given study, the decision has to be made which approach is considered as the primary endpoint. Why don't we analyze the data using both approaches? then we have to deal with the adjustment for multiplicity issue.
I used to make a comment and say "some regulatory authorities such as FDA recommend the simpler endpoint analysis"; then I was asked to provide the references to suport my statement. I did quite extensive search, but I could not find any real relevant reference. However, by reviewing 'statistical reviews' in the BLA and NDA in US, it is very rare to see any product approval based on the comparison of the slopes. Many product approvals are based on the comparison of 'change from baseline'.
So this is really a regulatory question. Every indication has their accepted endpoints so tradition takes precedence. According to my colleague, there is a movement in the Alzheimer's arena to look at differences in slopes, but this is basedon trying to claim disease modification. If this is the case, we may also apply this to the COPD area since for certain type of COPD, we can claim the disease modification by showing the differences in slopes.been used in COPD before?
On the other hand, It seems that that the slope model (random coefficient model) may be preferred in academic setting, but endpoint approach - change from baseline (with last value carried forward) may be more practical in the industry setting.
From statistical point of view, the slope approach makes a lot of sense, however, we need to be cautioned about some potential issues: 1. In some endpoint measure, there may be some type of plateau. If you reach that plateau prior to the end of the study there will be a loss of power comparing slopes as compared to some comparison of just the endpoint results or some type of general repeated measures assessment of the average treatment difference.2. If the slope comparison is used as the primary efficacy measure, the # of measurements per year on the primary efficacy variable is relevant. One may think that the more frequent measures will increase the power to show the treatmetn difference in slopes. The question arise when designing the study: are you choose a shorter trial with more frequent measures? or are you choose a longer trial with less frequent measures?

Geometric Statistics, geometric CV, intra-subject variation

In bioavailability and bioequivalence studies, the pharmacokinetic parameters (AUC, Cmax) are often assumed to follow the log normal distribution. Further about log-normal distribution.

The common technique is to calculate the geometric statistics (geometric mean, geometric CV and geometric SD). Notice that the geometric CV is independent of the geometric mean (unlike the arithmetic CV which is dependent on the arithmetic mean) and the geometric CV is used in the sample size calculation. When calculating the geometric statistics, the data in original scale is log-transformed, then anti-log to transform back.

In crossover design, the geometric CV can be estimated from the mixed model and is used to gauge the intra-subject variation. Geometric CV = sqrt(exp(std^2)-1) or CV=sqrt(exp(variance)-1) where the std^2 is estimated by the MSE. Variance is from ODS ‘CovParms’ table of SAS PROC MIXEd. Another variation is inter-subject CV and the std^2 is estimated by the variance estimate for the random subject effect from the proc mixed procedure.

It should be cautioned that Geometric CV sometimes is just being called CV or intra-subject variability. I heard that some large pharmaceutical companies include 'intra-subject variability' in the standard data presentation for pharmacokinetic parameters.

The topic about the CV, geometric CV was discussed in Boomer.org (http://www.boomer.org/pkin/PK06/PK2006512.html), a discussion mailing list on bioavailability and bioequivalences. Boomer.org used to be a great resource for PK-related discussion. However, recently the discussion group was dominated by a lot of the junkies posted by Indian guys. I guess it is because of the booming generic drug development industry in India.

Good Clinical Practice: A question & answer reference guide

I recently find the book edited by Parexel is extremely useful.

Good Clinical Practice: A Question & Answer Reference Guide
Edited by Mark P. Mathieu, Parexel Internationl Corporation
http://www.barnettinternational.com/ or
http://www.barnettinternational.com/EducationalServices_Publication.aspx?p=6544

Due to the fact that I work side by side with study managers and medical directors and due to my responsibility of overseeing the data management activities (outside of my responsibilities for biostatistics), I am involved in a lot of discussions the data collection, data quality. In a lot of situations, the decision has to be made on whether or not an event should be collected as an adverse events or how an event should be collected, ......

The Good Clinical Practice is just like the law. A lot of guidances really depends on how to interpret. The book of "A Question & Answer Reference Guide" is the one attempting to provide the interpretation of the GCPs with practical questions.

Here are two exmamples extracted from this book:

Q. Assuming that it is a study exclusion criterion, is a pregnancy while on study considered an AE? Is it considered an SAE?
A. In and of itself, a pregnancy is not considered an AE or SAE. However, abortion, whether accidental, therapeutic, or spontaneous, should always be classified as a SAE and expeditiously reported to the sponsor. Similarly, any congenital anomaly/birth defect in a child born to a female subject exposed to the investigational product should be recorded and reported as an SAE.
…..

Q. should expected clinical outcomes of the disease under study, which are efficacy endpoints, be reported as AEs/SAEs?
A. Some protocols instruct investigators to record and report all untoward events that occur during a study as AEs/SAEs, which could include common symptoms of the disease under study and/or other expected clinical outcomes. This approach enables frequency comparisons of all events between treatment groups, but can make event recording in the CRF burdensome, result in more expedited reports from investigators to sponsors, and fill safety database with many untoward events that most likely have no relationship to study treatment and that could obscure signal identification.
In some clinical trials, disease symptoms and/or other expected clinical outcomes associated with the disease under study, which might technically meet the ICH definition of an AE or SAE, are collected and assessed as efficacy parameters rather than safety parameters.
.....

==========
Recently, We have a study where several subjects had elective procedures (breast augmentation, mole removal,...). To show the diligence, we might be tempted to consider them as adverse events (even though they are not drug related), however, the elective procedures should not be considered as adverse events. These elective procedures can be collected on a separate CRF page, but should not be reported in AE page.

The best way is to specify the detail either in the study protocol or in the initial training provided to the investigational sites prior to the study start so that the same criteria are followed and all investigators are clear what should be reported and what should not be reported.

Are we become slaves of the Intent to Treat Principle?

The intent to treat (or intention to treat) principle was invented by the statistician about 30 years ago. It took a while for the clinical trial community to accept the this concept. Nowadays, the intent to treat principle has been well accepted by the people well beyond the statisticians. However, I don't think everybody really understand the concept even though he (or she) may mention the intent to treat pricinple every time he (or she) can. I have been really bothered by the comments from regulatory reviewers to suggest us to define an intent to treatment population for studies without randomization and without placebo or active control (for example, a dose escalation study). We seem to become slaves of the intent-to-treat.

In a lot of situations, the intent to treat principle is misunderstood. The intent-to-treat concept is tied with randomization for treatment allocation. No randomization, no Intent-to-treat.
The intent-to-treat concept is really for the large scale, confirmatory, pivitol studies. For very ealier stage studies (for example, the dose escalation studies) with very few subjects, there is no need to follow the intent-to-treat principle.

Intent to treat population includes all randomized patients in the groups to which they were randomly assigned, regardless of their adherence with the entry criteria, regardless of the treatment they actually received, and regardless of subsequent withdrawal from treatment or deviation from the protocol. Stricly according to the intent to treat principle, if a subject is randomized, but never receive study medication, the subject would be included in the statistical analysis; if a subject is randomized to drug A, but wrontly takes the drug B, the subject would be analyzed in treatment group A, not B (so called as randomized, not as treated); if a subject is randomized, but with no outcome measures, the subject would be included in the analysis with subject considered as treatment failure.

Intention to treat analyses are done to avoid the effects of crossover and drop-out, which may break the randomization to the treatment groups in a study. Intention to treat analysis provides information about the potential effects of treatment policy rather than on the potential effects of specific treatment.

To apply the intent to treat principle, an appropriate method for handling the missing data needs to be specified. A popular practical approach (not idea approach from statistical standpoint) is last value carried forward.

Intent to treat principle is not needed for all clinical trials and should not be interpreted as "include all enrolled subjects" or "all subjects who signed informed consent". The intent to treat is from the randomization standpoint, it has nothing to do with "study subject has intention to be treated in the clinical trial".

References:
1. ICH guidance E9 http://www.fda.gov/cder/guidance/ICH_E9-fnl.pdf
2. My presentation on ITT vs mITT http://webspace.webring.com/people/eu/um_3826/ITT_mITT_JSM2004.ppt
3. Wikipedian http://en.wikipedia.org/wiki/Intention_to_treat_analysis

Calculation of length of the study drug exposure

We have been using the following formula in calculating the length of the study drug exposure in many studies:

# of days of drug exposure = the last dose date - the first dose date + 1

However, this seems to be correct only if the subject receive daily dose of the study medication. We have many studies where the subject receive weekly infusion or every three weeks infusion of the study medication. In this situation, the above formula will underestimate the length of the study drug exposure.

The correct formula should be tied up with the dose interval.

If a subject receive weekly dose, the formula would be:
# of days of drug exposure = the last infusion date - the first infusion date + 7
or
# of weeks of drug exposure = (the last infusion date - the first infusion date + 7)/7

If a subject receive study drug every three weeks, the formula would be:
# of days of drug exposure = the last infusion date - the first infusion date + 21
or
# of weeks of drug exposure = (the last infusion date - the first infusion date + 21)/7

An early clinical trial with N=2

In the late 18th century, King Gustav III of Sweden decided that coffee was poison and ordered a clinical trial.

• The King condemned a convicted murderer to drink coffee every day.
• The control was another murderer who was condemned to drink tea daily.
• The outcome measure is 'death'.
• Two physicians were appointed to determine the outcome.

Results:

• The two doctors died first
• The king was murdered
• Both convicts enjoyed long life until the tea drinker died at age 83. (no age was given for the coffee drinker)

J Int Med. Oct 1991:289 - introduction to editorial from Nordic School of Public Health, Goteborg Sweden

Reprinted in Annal of Internal Medicine 1992: 117:30

Lack of clinical equipoise

Clinical equipoise provides the ethical basis for conduct of randomized clinical trials. This principal states that a clinical trial is acceptable only insofar as there is professional disagreement between researchers concerning uncertainty regarding the outcome of the study.1and thus even if a clinician prefers one arm over another, randomization is still sound when there are others who believe the other way around.

However, there are often different opinions between regulatory and investigator regarding the interpretation of equipoise and biases generated from publications suggestive of the efficacy of one product over another may cause lack of equipoise. Lack of clinical equipoise causes unwillingness at the investigator level to enroll patients because of strong belief by the majority of physicians in one treatment being superior over another. This results in difficultly in designing studies to support licensing a product such that physicians are unwilling to participate in a study that is necessary to satisfy regulatory agency(s) requirements for trial data demonstrating efficacy and safety.


References:
Freedman B: Equipoise and the ethics of clinical research. N Engl J Med 317: 141-145, 1987
Lilford RJ Declaratio of Helsinki should be strengthened. BMJ 322(7281) 299
Ashcroft R: Equipoise, knowledge and ethics in clinical research and practice. Bioethics 13 (3/4):314-326, 1999
Royall RM: Ethic and Statistics in Randomized Clinical trials. Statistical science 6(1): 52-66 1991

Phase 0 clinical trial

Traditionally, we have been talking about the phase I to phase IV clinical trials in drug development. We start from the small trials in healthy volunteers (phase I) to dose finding or proof of concept (POC) trials (phase II) to pivotal trials (Phase III), the post-marketing trial (Phase IV). Or we start from trials for MTD (maximal tolerable dose) - Phase I to trials for MED (minimal effective dose) - Phase II. Now there comes a new phase of clinical trial - Phase 0.
According to wikipedia, "Phase 0 is a recent designation for exploratory, first-in-human trials conducted in accordance with the U.S. Food and Drug Administration’s (FDA) 2006 Guidance on Exploratory Investigational New Drug (IND) Studies.[7] Phase 0 trials are also known as human microdosing studies and are designed to speed up the development of promising drugs or imaging agents by establishing very early on whether the drug or agent behaves in human subjects as was anticipated from preclinical studies. Distinctive features of Phase 0 trials include the administration of single subtherapeutic doses of the study drug to a small number of subjects (10 to 15) to gather preliminary data on the agent's pharmacokinetics (how the body processes the drug) and pharmacodynamics (how the drug works in the body).
A Phase 0 study gives no data on safety or efficacy, being by definition a dose too low to cause any therapeutic effect. Drug development companies carry out Phase 0 studies to rank drug candidates in order to decide which has the best PK parameters in humans to take forward into further development. They enable base go/no go decisions to be based on relevant human models instead of relying on animal data, which can be unpredictive and vary between species."

While the term 'phase 0' is fancy and novice, the usefulness of phase 0 trials needs to be proved in the future. At this point, I guess it is just a concept from governmental agencies such NCI (national cancer institute). I doubt that the industry will really be interested in this Phase 0 trial.

Translational Medicine

I have heard the term "evidence-based medicine", "socialized medicine", "individulized medicine", now there is a new term "translational medicine".

" Translational medicine is the continuum – often known as "bench to bedside" – by which the biomedical community takes a focused point of view to move research discoveries from the laboratory into clinical practice to diagnose and treat patients.

Translational medicine is often used synonymously with "Molecular Medicine" and "Personalized Medicine", both of which are used to refer to the process of applying molecular insights from laboratory discovery to clinical care.
Specifically, today’s process of translational medicine involves:

• A scientific search to discover the origins and mechanisms of disease
• The identification of and insight into specific biological events, biomarkers, or pathways of disease
• The use of such insights to systematically discover and develop new diagnostics and therapeutic methods and products
• The adoption of such new diagnostic and therapeutic approaches into the routine standard of care

Translational medicine represents a paradigm shift in the biomedical research enterprise. Traditionally, research, drug development, and clinical medicine were three virtually separate endeavors: bench scientists, drug developers, and clinical researchers rarely, if ever, met together, shared ideas, or even used the same vocabulary.

This dramatic change has come about in recent years as a result of the genomics and bioinformatics revolution. Patients provide the biospecimens from which "disease signatures" at the molecular level can be identified and are then used to develop diagnostics and drugs targeted at sub-groups of disease. The role of patient advocates has also been critical to this change in research and clinical care. They have catalyzed a more patient-centric approach to medicine."

A good example is the recent publication in Nature Medicine talking about the potential effect of Avandia on Osteoporosis. See the weblink below:

http://www.nature.com/nm/journal/vaop/ncurrent/abs/nm1672.html

A statement about interim analysis

I cite the following statement about the interim analysis due to two reasons:

1. Hazard ratio sometimes is very tricky. When hazard ratio is used, everything could be reversed, making the interpretation of the results difficult. In one of my studies, when hazard ratio is calculated for time to relapse, I have to calculate the hazard ratio for Placebo / Active to make the results explanable. In the example below, the greater the hazard ratio, the better. While it is still called 'non-inferiority', everything seems to be flipped.

2. It is interesting to see that the pre-specified alpha levels are used to avoid the calculation of the alpha spending function.

"Hypothesis:
The null hypothesis is that treatment with Drug A is inferior to treatment
with Drug B with respect to the duration of disease-free survival (HR >
1.305). The alternative hypothesis is that there is no difference between
treatment with Drug A and treatment with Drug B with respect to the duration
of disease-free survival (HR = 1).

Statistical Efficacy Analyses:
The two treatment groups will be compared for the duration of
disease-free survival based on the two sided 95% confidence interval for
the treatment disease-free survival hazard ratio from a Cox proportional
hazards regression model stratified for repeat TURBT (no/yes), high
grade papillary tumors (no/yes), CIS (no/yes), and region (North
America/Europe/Australia). Drug A will be considered to be non-inferior to
Drug B if the upper bound of the two sided 95% confidence interval for the
stratified disease-free survival hazard ratio of Drug A versus Drug B is below
1.305. Drug A will be considered to be superior to Drug B if the upper bound
of the two-sided 95% confidence interval for the stratified disease-free
survival hazard ratio of Drug A versus Drug B is below 1.0.

Interim Analyses:
Two planned interim analyses will be conducted by the DMC; one will be
performed six months prior to reaching the foreseen sample size of 811
patients and another when at least 50 percent of the expected efficacy
endpoints, defined as a diagnosis of non-muscle or muscle invasive
tumors or death, have occurred. Analysis will be limited to the
evaluation of futility and extreme efficacy. For the futility analysis
(or obvious treatment failure), a recommendation will be made to stop
the trial if the Primary Analysis is deemed futile at the p<0.001 level.
The extreme efficacy analysis will be assessed for success at the
p<0.0001 level for the Primary Analysis and a recommendation will be
made to stop the study. There will be no adjustment for overall alpha
spending for any of these analyses."

Categories of AE Frequency

A standard category of frequency for adverse drug reactions are provided in "Guidelines for Preparing Core Clinical-Safety Information on Drugs" - Report of CIOMS Working Group III (1995).
Very common >= 1/10 (>= 10%)
Common >= 1/100 and <>= 1% and < 10%)
Uncommon >= 1/1000 and <>= 0.1% and < 1%)
Rare >= 1/10,000 and <>= 0.01% and < 0.1%)
Very rare < 1/10,000 (< 0.01%)

CIOMS working group recognizes it is always difficult to estimate incidence on the basis of spontaneous reports, owing to the uncertainty inherent in estimating the denominator and degree of under-reporting. However, whenever possible, the AE frequency should be provided.

Core Safety Information

When reporting the adverse events in core safety information (CSI),
sometimes, the corporate faces a dilemma. On the one hand, due to the legal consideration, they may want to include all adverse events as many as possible so that nobody can say that certain side reactions are not warned if some bad things happen, on the other hand, over reporting/over inclusion are not suggested by CIOMS Working Group.

Routine inclusion of an extensive, indiscriminate list of adverse events is ill-advised for several reasons:

Differentiation: information included uncritically makes it more difficult to distinguish disease-related events or events that may be related to concomitant therapy from those that are due to the subject drug.

Dilution: over-inclusion can obscure or devalue the truly significant adverse experiences, thereby diluting the focus on important safety-information.

Mistake: by including "unsubstantiated" information, the physician may be led to do the "wrong" thing. For example, inclusion of an incompletely studies or ill-documented weak signal of a possible birth-defect could lead to unjustified abortion; overwarning for an important medical product could result in a change to a different medication not carrying the same type of warning, yet less safe or less effective.

Diversion: the inclusion of ill-substantiated information may discourage further spontaneous reporting of problems, which might have confirmed or clarified the extent and nature of the adverse event.

Clutter: ease of reading and understanding is critical; the fewer words and the less extraneous information the better.

Crossover trials should not be used to test treatments when negative correlation exists

I recently read a book by T.J. Cleophas titled "Statistics Applied to Clinical Trials". It is interesting that the author em phased the importance that the crossover study should not be used to test treatments with different chemical class.

"..Clinical trials comparing treatments with a totally different chemical class/mode of action are at risk of negative correlation between treatment responses. Such negative correlations have to be added to the standard errors in a cross-over trial, thus reducing the sensitivity of testing differences, making the design a flawed method for evaluating new treatments. "
"So far, statisticians have assumed that a negative correlation in cross-over studies was virtually non-existent, because one subject is used for comparison of two treatments. For example, Grieve recently stated one should not contemplate a cross-over design if there is any likelihood of correlation not being positive. The examples in the current paper show, however, that with completely different treatments, the risk of a negative correlation is a real possibility, and that it does give rise to erroneously negative studies. It makes sense, therefore, to restate Grieve's statement as follows: one should not contemplate a cross-over design if treatments with a totally different chemical class/mode of action are to be compared."
"At the same time, however, we should admit that the cross-over design is very sensitive for comparing treatments of one class and presumably one mode of action. The positive correlation in such treatment comparisons adds sensitivity, similarly to the way it reduces sensitivity with negative correlations: the pooled SEM is approximately sqrt(1-r) times smaller with positive correlation than it would have been with a zero correlation (parallel-group study), and this increases the probability level of testing accordingly. This means that the cross-over is a very sensitive method for evaluating studies with presumable positive correlation between treatment responses, and that there is, thus, room left for this study design in drug research."

One example the author mentioned is Ferrous sulphate and folic acid used for improving hemoglobin. There was an inverse correlation between the two treatments: Ferrous sulphate was only beneficial when folic acid was not, and so was folic acid when ferrous sulphate was not.

Measure Enrollment Imbalance

Question:

"A Sponsor PM would like to know how many subjects can be enrolled at their largest-enrolling site before it begins to skew the study results. She says a previous CRO was able to calculate this number for her."

My response:

"I don't think we really need to calculate the probability to get to the answer. There may be no easy way to calculate the probabilities.

It depends on # of subjects for the study and # of sites. I typically divide the # of total subjects by # of sites to get an average # of subjects per site. Then you truly believe that there may be the site difference, you could choose a cut point (arbitrary) of 3-5 times the average # of subjects. For example, if a study is intended to enroll total 100 subjects at 10 sites, the average will be 10 subject per site.

I will probably choose a number (30, 40, or 50) as a cut point as a cap for maximum # of subject a site can enroll."

Question: Many assume that the FDA advocates that the subjects enrolled in any clinical trials be well dispersed among study sites involved in a particular clinical program. Does the FDA have any guidance, rules of thumb, or limits regarding severe imbalances in enrollment between sites?

Answer: In an informal response to this question, the FDA noted that "it does have concerns about how many patients are enrolled in studies from specific study sites. The most important issue [is] that all sites conducting the research use the same protocol. Sometimes this requirement for using the same protocol can be an issue that requires input by FDA's review division because different standards of care (i.e., standard treatments that are typically used within a particular country for the treatment of various cancers) exist in different countries. As long as the protocol is being followed, the studies are conducted in conformance with good clinical practice, and the study/study records can be audited by FDA, differences in recruitment at the various sites do not present a problem. FDA does not require specific enrollment levels at specific sites."