In epilepsy trials, there often is interest in conducting a pharmacokinetic (PK) analysis by regressing the plasma concentrations of drug exposure on the primary seizure outcome/endpoint.

For example, an RCT has 4 treatment arms (1:1:1:1 randomization to placebo, dose level 1, dose level 2, and dose level 3). In addition to the typical treatment comparisons of each active arm to placebo, one would substitute the plasma concentrations of the actual drug exposure (continuous values) with treatment group and drop all placebo subjects (as their plasma concentrations would be 0), and run a regression on the seizure endpoint for the active subjects.

This type of analysis seems to be commonly performed for epilepsy trials, but I’m not sure if it makes sense. Any feedback would be greatly appreciated.

Thank you, Prof. Harrell. I agree that the placebo subjects should not be dropped from the PK analysis.

Is the estimated coefficient (ie, the slope, along with its CI and p value) of the continuous PK variable the only useful information for interpretation here? Asking this because overlaying the observed values on top of the regression line will look a bit funny since all placebo subjects will have a value of 0 for their PK parameter.

Unfortunately, there is a small amount of missingness for the PK values. Is the concern related to bias due to deviating from the randomized population?

Another approach I’ve seen is substituting the treatment arms with the dose level as a continuous variable: for example, setting the placebo arm to 0 mg, and active arms to 20 mg, 30 mg, and 40 mg for the regression. Does this approach add any value?

There are several interesting issues about this design and I hope you’ll share some results. Yes the missingness is about possibly breaking the randomization. You need to be completely sure that the missingness is not because of anything related to the patient post-randomization.

There is nothing odd about having a bunch of 0s in the graph, but do allow the relationship to be nonlinear. The only real difficulty is that with clumping at zero it’s hard to specify knot locations in a regression spline. You might put the first knot at the lowest concentration observed in non-placebo patients, and 3 other knots at 0.25 0.5 0.96 quantiles of observed concentrations above that.

Concerning analyses of intended doses, one of several useful analyses might be to do this:

Fit a model with smooth nonlinear effects (e.g. regression splines) of both dose and concentration.

Run a likelihood ratio \chi^2 chunk test to estimate how much outcome variation there is due to concentration over and above the variation explained by dose.

Make sure that the LR \chi^2 of dose adjusted for concentration is close to zero, otherwise you’ll need to explain how the dose effect is not explained by concentration.

Is there a potential issue here re: collider bias similar to ITT vs per protocol since the actual plasma concentration seems a bit like a mix of per protocol effect + individual differences in drug metabolization? I’ve seen some dose level meta-analysis models (eg CRAN - Package MBNMAdose) which I imagine are adapted from individual level models so they may cite some relevant literature that could be helpful.

I think there is some small risk of a collider bias, which is why dose-response analysis (dose vs. clinical outcomes) is emphasized. But the analyses incorporating achieved blood concentration will be extremely helpful.

Thank you for your feedback, Prof. Harrell. What are the issues one should be aware of for this design (as you mentioned there are several interesting issues)?

I tried the following using:

treatment group: endpoint = baseline seizure + treatment group

both continuous dose and continuous concentration (smooth nonlinear): endpoint = baseline seizure + rcs(concentration, as above) + rcs(dose, c(20,30,40))

General observations:

Approaches 1), 2) and 3) have similar R-squared and adjusted R-squared values. Interpretation is more straightforward for 1) when endpoint and baseline values are natural log transformed.

For figures, it seems that the baseline seizure variable needs to be removed from the model, otherwise the curves won’t look smooth. And the more predictors added, the more zigzagged the curves will be.

Comparing 5) to 4)

lrtest(model_4, model_5) shows a likelihood ratio χ2 close to 0.

1- var(predict(model_4, type=‘response’)) / var(predict(model_5, type=‘response’)) = close to 0

Seems like the take-home message is: once adjusted for dose effect, there’s no value added by further adjusting for concentration. The reverse is also true: once adjusted for concentration effect, no value is added by adjusting for dose.

Comments regarding the choice of endpoint based on some modelling attempts:

Modeling on percent change from baseline (PCHG) tends to get poor adjusted R-squared values. Not a surprise knowing PCHG is not a valid endpoint for statistical analysis but unfortunately it continues to prevail as an FDA approved endpoint.

Adjusted R-squares look much better using natural log transformed seizures at baseline and follow-up, instead of PCHG.

Modelling on daily seizures using a Markov PO ordinal logistic model seems to be a more promising approach.

I’m a patient advocate, previously a CIRB member for adult early phase cancer trials, but have no experience with epilepsy. Are there any ethical concerns surrounding the use of placebo as controls for this indication?

Are you asking if patients with epilepsy assigned to the placebo arm are completely off medications? My understanding is that they would be on a standard treatment, and the investigational drug would be considered as adjunctive therapy.