Bioequivalence and Bioavailability Forum

Dear D. Labes!

❝ I can not get the point. What has the failed study to do with the study now showing BE? The formulation for which now BE is claimed is the reformulated, a new product.

❝ Generalizing this would mean that all unsuccessfull efforts and attempts during pharmacists or other work within the development must be reported.

Exactly! See Section 4.1 (page 5, lines 142-144):
'The clinical overview [...] should list all studies carried out with the product applied for. All bioequivalence studies [...] must be submitted.'

❝ Evaluation of data from several bioequivalence studies, page 13/14 (lines 537-542)

❝ '2. [...] It is not acceptable to pool together two ambigous studies to reach a positive conclusion.'

❝ This may be ok from the regulators point of view (He would like to see at least one study showing BE), but it is against all principles of a meta analysis. Pooling together studies and obtaining a clearer picture is why meta analysis was invented.

An anecdote from my side to lift your mood:
Recently we had a discussion with one of the members of the 'pharmacokinetolophystic subgroup' (^©2008 by ElMaestro) about a hypothetical example.
Study 1 in 24 subjects; 1 subject showing a low response of the reference, not BE due to variability higher than the one used in sample size planing. BE in nonparametric analysis and additional parametric analysis after removal of the outlier (even if planned in the protocol): --> not acceptable
Study 2 is Study 1 repeated in the same 24 subjects; the outlying subject from Study 1 shows a 'normal' response, BE demonstrated: --> acceptable, even if the regulator knows of Study 1.
Why? We have a tendency to believe in repeated values (just think about laboratory screenings). Maybe results seen in Study 2 were just by chance and Study 1 'correct' (subpopulation?).
Anyhow, pooling of Studies 1 & 2: --> not acceptable
Again, why?
Study 3 in 48 subjects; 1 subject showing a low response of the reference, but BE demonstrated due to lower (by sqrt(2)) variability as compared to Study 1: --> acceptable

Do you get the idea?

4.1.2 Reference and test product (page 6, lines 193-194)
'When variations to a generic product are made, the comparative medicinal product for the bioequivalence study should be the reference medicinal product.'
IMHO, this a very good idea - nothing was stated about it in the 'old' NfG, and I think generally once a generic was approved, variations were studied in comparison to the company's own product - not the innovator.
Lines 202-207 are also a good idea - although a difference in content of more than 5% is rarely seen - it protects against surprises in the biostudy if ±5% are used in sample size planing.

4.1.2 Reference and test product (page 7, lines 218-220)
'The study sponsor will have to retain a sufficient number of all investigational product samples in the study for one year in excess of the accepted shelf life or two years after completion of the trial or until approval whichever is longer to allow re-testing, if it is requested by the authorities.'
Fine. And if a request comes, what about the results of re-testing years after the shelf life? Back-extrapolate with the parameters found in stability testing for the IMPs - endless discussions approaching.

Dear All,

I have one query regarding the lines mentioned below.

It is acceptable to use a two-stage approach when attempting to demonstrate bioequivalence. An initial group of subjects can be treated and their data analysed. If bioequivalence has not been demonstrated an additional group can be recruited and the results from both groups combined in a final analysis. [Line 564-566, Page 14]

Now my question is: Suppose when data corresponding to initial group of subjects is analysed, it demonstrates Bioequivalence. Then what is to be done. We still have to go for additional group of subjects as mentioned in the protocol or we can stop at first step? Suppose we stop at first stage in that case whether study will be accepted by EMEA or not?

Thanks and Regards,

Dear all,

Here is another one:

On page 5, line 150-151 — the criterion for "adequate wash-out period" is not defined. However, in the previous 2001 NfG, for steady-state designs, it was given as "at least 3-times the terminal half-life". In FDA's 2003 GfI, an adequate washout period was described as "e.g., more than 5 half lives of the moieties to be measured".

Do you think they forgot to define it.. or?

Regards,

Dear D. Labes!

❝ '[...] As C_max at steady state may be less sensitive to differences in the absorption rate than C_max after single dose, bioequivalence should, if possible, be determined for C_max after single dose administration (i.e. after the first dose [...]).'

❝

❝ The last sentence excludes one of the possibilities for dealing with HVD's, namly a steady state study to reduce variability in C_max in comparision to the single dose variability (if this is possible for the formulation under consideration).

Exactly. From a PK point of view it's possible to show that C_max is less sensitive to differences then AUC if going from single dose to steady state (this statement is also given in the earlier sentence). For HVDs the option to go for steady state was eliminated for AUC (use a replicate design instead - which does not reduce the variability per se; since scaling is not allowed - large studies are approaching!), but left here if it's simply not possible to characterize the profile due to analytical problems. Since C_max is less sensitive, any attempt should be made to 'catch' C_max in single dose. Another example from the past are bisphosponates, where amount excreted in urine was accepted for extent of BA, but still C_max from plasma was required by some countries' regulators.

❝ It is required by this sentence that the whole concentration time course of the first dose has to be followed up by a sufficient sampling schedule.

I don't think it does make sense to sample the entire profile, when you already know beforehand that you cannot come up with results >LLOQ in the later time points. But the conditions given somewhere else in the Guideline about selection of time points for the characterization of C_max/t_max apply.

❝ This is in practice essentially the request of doing two studies: single dose and multiple dose, although combined.

Yes. Not only from the Guideline, but also from personal communications I had with some of the authors.

❝ It remains the secret of the authors of this DRAFT why the first dose C_max should be a suitable metric or should be better in detecting differences in case of "... problems of sensitivity of the analytical method precludes sufficiently precise plasma concentration measurements after single dose administration ..."

As mentioned above it's possible to show it by simulations. I have the references somewhere, but since I'm leaving for vacation tommorow - it must wait until Sep 17^th earliest.
But you can do it on your own: Fire up some PK software (even M$-Excel would do the job) - define parameters of two hypothetical formulations in such a way that C_max is let's say 10% apart - go into steady state - the difference should be smaller.

Dear D. Labes!

❝ Statistical analysis, page 13 (lines 504-505)

❝ A nonparametric analysis is not acceptable.

❝

❝ This cannot be discussed seriously without crying.

Join the party. In the past I have evaluated about 300 BE studies nonparametrically (additive model for t_max, multiplicative for AUC and C_max); ANOVA was only given in an annex essentially to get the CV and have a look whether my sample size assumptions turned out to be justified and have it ready for future studies. Sometimes I was asked to make the ANOVA the primary analysis post hoc. This was the crying phase.
Later on driven by both regulators and sponsors I retreated to:

• nonparametric analysis for t_max
  
• decision tree about the type of analysis based on intra-subject residuals
  • parametric if p(Shapiro-Wilk)>0.05
    
  • nonparametric if p(Shapiro-Wilk)≤0.05

This was the screaming phase (but covered by ICH-E9):

‘In the choice of statistical methods due attention should be paid to the statistical distribution […]. When making this choice (for example between parametric and non-parametric methods) it is important to bear in mind the need to provide statistical estimates of the size of treatment effects together with confidence intervals […].’

Since regulators hate pretesting (even one of the advocates of nonparametrics in the field of BE, Dieter Hauschke wouldn't do it), right now I'm with nonparametrics for t_max, parametrics for AUC and C_max. Still I'm looking at the residuals. Quoting Jones and Kenward (Design and Analysis of Cross-Over Trials, 2^nd ed. 2003):

“No analysis is complete until the assumptions that have been made in the modeling have been checked. Among the assumptions are that the repeated measurements on each subject are independent, normally distributed random variables with equal variances. Perhaps the most important advantage of formally fitting a linear model is that diagnostic information on the validity of the assumed model can be obtained. These assumptions can be most easily checked by analyzing the residuals.”

In the worst case I present two evaluations; a full data set and another one with the potential outlier removed (only if it’s a failure of the reference). But this is unplanned and stupid anyway.
This is the current phase of hating pragmatism.

But the new Guideline will lift any need for thinking from my side; being part of the flock I only have to follow the shepherd to be happy.

❝ Also note that MRT has disappeared.

Interesting. Maybe, because the Guideline deals only with IR formulations - and the group didn't consider it of any importance? For MR formulations there’s a reference to CPMP/EWP/280/96 included.

❝ Newly mentioned is LambdaZ, which is nearly the same, but on an inverse scale, as half live t_1/2.

Yes, but how to deal with it? Strictly speaking, if half lives are different - BE testing does not make sense. For an IR formulation both AUC and C_max should be influenced only by absorption; elimination is drug-specific. If the apparent elimination is different, it would mean that we are trapped by flip-flop PK, i.e., the late phase of the profile represents absoption rather than elimination. In such a case the main parameter AUC_t and the last sampling at 72 hours are debatable.
What should we do now? Come up with some descriptive statistics and , or run a pretest to show there's no difference before proceeding? If yes, what’s the distribution of lambda_Z/t_1/2? I used to give the harmonic means^* in a table - but I’m not sure about a transformation useful in a comparison…

---

• Lam, FC, Hung, CT and DG Perrier
  Estimation of Variance for Harmonic Half-Lives
  J Pharm Sci 74/2, 229–31 (1985)

Dear DLabes!

❝ Statistical analysis, page 13 (lines 504-505)

❝ A nonparametric analysis is not acceptable.

❝

❝ This cannot be discussed seriously without crying.

❝ Moreover in the text any statistical analysis of t_max has be gone.

Some more background information…
Quoting an e-mail I received from Walter Hauck: “Also interesting that they now say they will not accept non-parametric analyses. That seems a step backwards.”
I talked to a lot of regulators at the EGA-CMP(h)-Symposium in Paris last week and what we already suspected is true: Nonparametrics are evil, therefore t_max had to eliminated from the PK-metrics as well. We all know that t_max is a lousy metric for the rate of absorption, but on the other hand it served well in thousands of studies in the past. Although introduced as a metric for ‘early exposure’ by the http://www.fda.gov/cder/guidance/5356fnl.pdf FDA in 2003, to my knowledge there’s no empirical evidence that this metric performs better than t_max.

Schall and Luus (1992)¹ have shown that in the one-compartment open model the difference in t_max, and the ratio of the C_max/AUC ratio of two drug formulations are equivalent characteristics for the comparison of the absorption rate. In two- or higher compartment models these relationships hold approximately. This provides a powerful argument for the use of the observed C_max/AUC ratio, rather than t_max, as a mesure for the rate of absorption, because it is well-known that C_max/AUC can be observed with higher precision than t_max.
Midha et al. (1994)² suggested that mean AUC_tmax may not be a reliable basis for estimation of relative extent [sic!] of absorption because the within-subject variabilities of the partial areas over the first few hours after dose tend to be very high, but decline rapidly to become stable at some point that may fall before or after mean-t_max.
Midha et al. (1993)³ showed that high within-subject variability increases the likelihood of failure of 90% confidence intervals to fall within preset bioequivalence limits in simulations in which the true ratio of geometric means was set at unity.
In a retrospective analysis of 11 BE studies early partial areas showed high variability which stabilized at about 2×t_max, which lead the authors to their often quoted statement: “Once absorption is over, formulation differences no longer apply.”⁴

1. R Schall and HG Luus
   Comparison of absorption rates in bioequivalence studies of immediate release drug formulations
   Int J Clin Pharm Ther Toxicol 30/5, 153–9 (1992)
   
2. Midha KK, Hubbard JW, Rawson MJ, and L Gavalas
   The application of partial areas in the assessment of rate and extent of absorption in bioequivalence studies of conventional release products: Experimental evidence
   Eur J Pharm Sci 2, 351–63 (1994)
   
3. Midha KK, Hubbard JW, Yeung PKF, Ormsby E, McKay G, Hawes EM, Korchinski ED, Gurnsey T, Rawson M, and R Schwedes
   Application of Replicate Design
   In: KK Midha and HH Blume
   Bio-International: Bioavailability, Bioequivalence and Pharmacokinetics
   medpharm Scientific Publishers, Stuttgart, pp 53–68 (1993)
   
4. Midha KK, Hubbard JW, and MJ Rawson
   Retrospective evaluation of relative extent of absorption by the use of partial areas under plasma conentration versus time curves in bioequivalence studies on conventional release products
   Eur J Pharm Sci 4, 381–4 (1996)

If partial AUC truncated at reference’s t_max will become a main target parameter (according to statements at the EGA-Symposium no widening of the acceptance range of 0.80-1.25 will be considered), this metric will lead to exceptionally high sample sizes because of its intrinsic variability.

In the following two examples from my database (IR formulations, clinical claim on C_max/t_max). Both of them showed very low to moderate CV_intra on both AUC and C_max, and were suitably powered in order to be able to demonstrate BE for C_max.

Example 1:
Original evaluation
Median t_max (ref.) 1.5h
Additive model (nonparametric)
Hodges-Lehman estimate: ±0.00h (100%)
Moses CI: -0.25, +0.25 (85.0%, 115%)
Conclusion: BE
New evaluation
pAUC_1.5
Multiplicative model (parametric)
GMR: 90.1%
CI: 75.0%, 110.1%
CV_intra 26.4% (AUC_t 13.3%, C_max 17.0%)
Conclusion: not BE

Example 2:
Median t_max (ref.) 1.5h
Additive model (nonparametric)
Hodges-Lehman estimate: +0.26h (116%)
Moses CI: ±0.00, +0.50 (100%, 130%)
Conclusion: not BE
pAUC_1.5
Multiplicative model (parametric)
GMR: 66.1%
CI: 53.1%, 82.0%
CV_intra 29.7% (AUC_t 6.33%, C_max 9.43%)
Conclusion: not BE

Power to show BE for partial AUC was clearly insufficient, even in example 1. CV_intra for the partial AUC was thrice that of C_max and almost five times that of AUC_t in example 2.

---

Edit: FDA-link corrected to latest archived copy. [Helmut]

Dear Janmacek,

Oh, I couldn't agree more with you. This requirement is counter-productive, will not meet its objective, will be a pain in the ass for everybody, and nobody has an idea on what the agencies are going to do with it .

You are right: the "automatic" integration is performed using user-defined parameters anyway. You will always have incorrectly integrated chromatograms, unless you are dealing with high concentrations with very regular peak shapes. It is perfectly legitimate to re-integrate chromatograms, and as you mention, you can't consider "automatic" integration as "gold standard", and manual integration as systematic evil. Some time ago the people from AB/MDS Sciex made a comparison between the 3 integration algorithms in Analyst and manual integration. The conclusion was that manual integration was time consuming and a little less reproducible, but it gave the best results (at least with trained personnel).

I would consider this requirement as counter-productive: the analytical labs will be reluctant to re-integrate chromatograms, in order to reduce the paperwork and because they will be afraid of getting into trouble. The general opinion will be that EMEA does not want chromatograms to be re-integrated (I have already heard a number of CROs say they don't re-integrate chromatograms because FDA does not like it). The consequence will be that we will have concentrations in the reports calculated from poorly integrated whromatograms.

Asking for the initial concentration to be reported in addition to the concentration after re-integration is stupid: if you need to re-integrate the chromatogram, it means that the initial concentration is not reliable ! So why put an unreliable concentration in the report ?

This requirement will not prevent fraud: it will not give any information on whether the new integration is correct or not. The guideline does not require to submit the "old" and "new" integration. And even if the "new" integration was submitted: it can be very difficult to say whether an integration is "correct" or "incorrect", unless it is grossly manipulated. Have the same chromatogram integrated by 10 different analysts, and you will get 10 different integrations, all of which may be acceptable. The real question is whether all chromatograms have been integrated in the same way: standards, QCs, and subject samples. To really check the integration of a single re-integrated chromatogram, you may need to look at all other in the same run.

And anyway if a lab wants to manipulate chromatogram integrations, what difference will the table make ? They may not mention the manipulated integrations in the table, and nobody will see it unless there is an inspection. The table will make no difference from the current situation: inspectors will look at the integrations anyway, whether they have this table or not.

Anyway, what difference does it make if you have 1 %, 5 % or 20 % of re-integrated chromatograms ? 1 % can be enough to validate failing runs. 1 % can be a lot, and 10 % very few, depending on the look of your chromatograms, on your LLOQ and on your background noise.

So this requirement will make no difference for bad labs, and will be hell for the good ones...

❝ The above mentioned requirement will increase workload in the analytical laboratory as for re-integrated chromatograms two copies should be stored in the archive - one with bad integration and the second with correct one.

Well, you're already supposed to do that, if you are using paper raw data. Nothing new here.

Regards
Ohlbe

Dear DLabes,

❝ As is known in the standard 2x2 cross-over subjects with missing data do not contribute to the ratio or difference of Test versus Reference. Only the variability is affected, usually to a minor extent.

I'm not sure I get your point there. In a standard 2x2 cross-over trial, the new version of the guideline would still allow subjects missing one of the two periods to be excluded.

❝ 'All treated subjects should be included in the statistical analysis, with the exception of subjects in a crossover trial who do not complete at least one period receiving each of the test and reference products (or who fail to complete the single period in a parallel group trial)'.

IMHO this would apply in the case of a trial with 3 treatments or more (include subjects for whom you have data for at least one reference product and one test product) or replicate design trials (include subjects who have completed at least one period for the test and one for the reference).

Regards
Ohlbe

Dear HS!

I think your confusion is a consequence of "scientific sound" and "well-established alternatives" which in "certain cases" are "adequate" or "appropriate" and "may be" .

OK, the regulators want to see the variability under reference treatment to judge it is a HVD. And this can only be shown in a replicate design.
Although one has to be cautious: In my experience models with same variability of test and reference often fit the data of replicate studies as well.

But if it is HVD, it has no consequences! No scaling, but only a marginal widening of the bioequivalence range, appropriate only to moderate variability.

Moreover their reasoning is not very "scientifically sound": If C_max has no importance for clinical efficacy and safety, why to have a BE limit to meet at all?

And if we talk about HVDs, why is an adjustment for AUC not allowed? We all know HVDs with high variability in AUC also. And there are brand names of them on the market!
With this guidance (if it comes unchanged) it will be very hard to generic substitute them (only studies with hundreds of volunteers will do it) .

To my humble opinion this part of the DRAFT totally neglects all the discussions about HVDs in the scientific community and in the USA and Canada regulatory bodies. This will lead in the near future to diverging guidelines I guess. It's a pity.

Dear all!

❝ 4.1.10 Highly variable drugs or drug products, page 16 (lines 631-641)

According to discussions at last week's EUFEPS workshop members of EMEA's PK-group unanimously expressed their point of view as following:
If the reference formulation is suspected to be a HVDP and no clinical reasons speak against widening of the acceptance range for C_max the pivotal BE-study may be started right away in a replicate design (no pilot to demonstrate a HVDP reference followed by a pivotal study to show BE). It is unacceptable to run a two-period study of the reference alone, because regulators suspect that the performance of such a study will be intentionally sloppy in order to obtain a high CV.
The study should be powered to demonstrate BE for the conventional BE-range if CV<30%. If in the study CV>30% the acceptance range may be widened to 75%-133%.
Example (expected PE 0.95, 80% power):
CV%    2-way       3-way replicate       4-way replicate
      80%-125%   80%-125%   75%-133%   80%-125%   75%-133%
 30   40 ( 80)   30 ( 90)   18 ( 54)   20 ( 80)   12 ( 48)
 40   66 (132)   50 (150)   28 ( 84)   34 (136)   20 ( 80)
 50   98 (196)   74 (222)   42 (126)   50 (200)   28 (112)
 60  134 (268)  102 (306)   56 (168)   68 (272)   38 (152)
 70  174 (348)  130 (390)   72 (216)   88 (352)   48 (192)
 80  214 (428)  162 (486)   90 (270)  108 (432)   60 (240)
 90  258 (516)  194 (582)  108 (324)  130 (520)   72 (288)
100  300 (600)  226 (678)  124 (372)  150 (600)   84 (336)
The table gives samples sizes and number of treatments (which are a rough estimate of study costs). Though more treatments are needed in 3-way design, one must expect higher drop-out rates in 4-way design.
The draft defines (line 639) the limit of a HVDP with CV>30%, whereas generally a cut-off of CV≥30% is used. Hopefully this definition will change in the final version.

Going deeper in the example: You suspect that the CV will be 40%. Since you are not sure, you should power your study for 80%-125% (CV<30%). The sample sizes will be 50 (150 treatments) in a 3-way replicate and 34 (136 treatments) in a 4-way replicate. If it turns out that CV=30% you are powered with 95% to demonstrate BE within the conventional range - since you (mis-)used 50 subjects instead of the needed 30. If CV=40% as expected you may widen the acceptance range and are powered with 99.8% (or for 80% power your PE may lie with 85.4%-117.1%). You may also have performed the study as a conventional 2x2 in 66 subjects (with fewer treatments). IMHO the only gain is the larger allowed deviation from the reference. I'm not sure whether this was the primary intention of the 'inventors' or maybe I'm misunderstanding something terribly...

P.S.: In the US with RSABE you probably would perform the study as a 3-way replicate design in 34 subjects independent from the CV...

Dear all!

❝ […] but we are not allowed to exclude outliers anyway.

Really?
According to the recent Q&A-document:

'[…] erratic concentration profiles (either non-existing or extremely delayed) can be obtained. Therefore the sampling period should be designed such that measurable concentrations are obtained, taking into consideration not only the half-life of the drug but the possible occurrence of this effect as well. This should reduce the risk of obtaining incomplete concentration-time profiles due to delay to the most possible extent. These effects are highly dependent on individual behaviour. Therefore, but only under the conditions that sampling times are designed to identify very delayed absorption and that the incidence of this outlier behaviour is observed with a comparable frequency in both, test and reference products, these incomplete profiles can be excluded from statistical analysis provided that it has been considered in the study protocol.'

My emphases.

In other words, if you see an outlier after the reference, cross your fingers to have another one after the test as well. That's true equivalence: a bad test to a bad reference.
Or should we do some statistics? Which one? Maybe Fisher’s exact test? For 24 subjects it will need 5 outliers in one formulation to get a significant difference (p 0.0496) to none in the other formulation…

Dear all!

The Draft was presented by a representative of the Swedish Authority at the Dissolution/BA/BE-Conference in Prague last week. When asked about the '500 ml' she replied 'Oh, I did not realized that; I think, that's a typing error.' On the other hand I heard about deficiency letters already issued by the Spanish Authority to two different companies asking for dissolution data 'compliant with 500 ml'...
Quoting this issue at the EGA-CMP(h)-Symposium in Paris gained a lot of laughter. Everybody should be aware that only two documents are binding, namely the NfG on BA/BE (2001) and the Q&A (2006) until release of the final version of the BE-Guideline, which is expected for the late autumn 2009 at the earliest.