The therapeutic window is a range of dose concentrations that will provide an effective response without significant adverse effects. Therefore, studies are designed to carefully determine the dose given to patients so that the concentration of the drug in the human body will fall into the therapeutic window. If the dose is too low, the drug might not be effective. However, if the dose is too high, adverse events might harm the human body.

Therefore, it is essential to precisely predict the drug concentration based on a given dose. Generally, there are three possible relationships between drug concentration and drug dose: (1) Increasing doses will result in a proportional increase in drug concentration. (2) Increasing doses will result in more than proportional increase in drug concentration. (3) Increasing doses will result in less than proportional increase in drug concentration. Among three relationships, (1) represents when dose proportionality is achieved. If dose proportionality is achieved, predicting the drug concentration will be much easier for future applications.

There are many methods to model the relationship between concentration and dose. The power model [13] is one of the most wildly used. It assumes that the logarithm of the pharmacokinetic ( P K) parameter is linearly related to logarithm of dose. The PK parameter can be C m a x or AUC for single dose, or C s t e a d y s t a t e for multiple doses. The formula can be written as l n ( P K ) = β 0 + β 1 l n ( d o s e ). The equation can also be rewritten without the natural log as P K = e β 0 d o s e β 1 .

Assuming the maximum dose is h, and the minimum dose is l, P K h P K l = e β 0 h β 1 e β 0 l β 1 = h β 1 l β 1 = ( h l ) β 1 = r β 1 . If β 1 = 1, we can obtain P K h P K l = h l . This means that, if the dose is doubled, the drug concentration is also doubled. In other words, dose proportionality is achieved.

In the traditional comparative research study, hypotheses are often proposed to compare a new therapy to a current therapy (two arms) or a meaningful value (single arm) to detect any difference. Therefore, the null hypothesis is that there is no difference between new therapy and the current therapy, or the meaningful value, and the alternative hypothesis is that there is a difference. However, if we apply this approach to the assessment of dose proportionality, rejecting the null hypothesis β 1 = 1 is equivalent to claiming alternative hypothesis β 1 ≠ 1 is true.

Therefore, this logic is not appropriate for establishing dose proportionality since we need to prove that β 1 = 1 to establish dose proportionality. Assuming β 1 ≠ 1, strong evidence is needed to reject this assumption. Therefore, we cannot use the traditional comparative hypothesis.

Instead, equivalence testing is suitable for our context. The simplest and most common way is to use the two one-sided test (TOST) procedure described by [26]. It is defined by two margins ( θ l , θ h ) at the left and right side of the value that indicates equivalence. One then performs two one-sided tests at a desired α level: (1) H 0 : θ ≤ θ l versus H 1 : θ > θ l , and (2) H 0 : θ ≥ θ h versus H 1 : θ < θ h . This process is equivalent to calculating a ( 1 − 2 α ) ×100% confidence interval for θ and determining if it lies entirely between θ l and θ h .

Assessment of dose proportionality is ultimately a kind of equivalence test. We want to test H 0 : r β 1 − 1 < = θ l or r β 1 − 1 > = θ h versus H 1 : θ l < r β 1 − 1 < θ h . This is equivalent to testing if 1 + l n θ l l n r < β 1 < 1 + l n θ h l n r . The U.S. Food and Drug Administration defined θ l = 0.8 and θ h =1/ θ l =1.25 [9]. When the ( 1 − 2 α ) ×100% CI with α = 0.05 for parameter β 1 , which is the slope for dose, falls between 1 − 0.223 l n r < β 1 < 1 + 0.223 l n r , dose proportionality is established.

In k-total analyses, the α 1 , α 2 , … , α k are spent across different interim analyses to maintain the total α level. For frequentist methods, the confidence interval for β 1 is established at ith interim analysis by calculating ( 1 − 2 α i ) ×100% confidence interval [8]. For Bayesian methods, the credible interval ( L ϵ 1 , U ϵ 1 ) for β 1 is established at ith interim analysis by calculating P ( θ < L ϵ 1 ) = ϵ 1 and P ( θ > L ϵ 2 ) = ϵ 2 [11]. We set ϵ 1 + ϵ 2 = 2 α i . And bioequivalence is established if ( L ϵ 1 , U ϵ 1 ) falls between 1 + l n θ l l n r and 1 + l n θ h l n r . While there are many choices of the credible interval, we consider high density intervals (HDI) for the remainder of this manuscript.

First we briefly review the multisource exchangeability model [16]. Assuming there are two historical data sources ( D 1 , D 2 ) and one primary study D p , where D represents the observed data, there will be 4 assumed exchangeability patterns ( Ω 1 , Ω 2 , Ω 3 , Ω 4 ) since H = 2 and K = 2 2 . For each exchangeability configuration, there will be a posterior weight estimated for its appropriateness of assuming exchangeability with the current trial, and the final model will be a weighted sum of the models. For two historical data sources, the final model utilized for inference will be q ( β | D p , D 1 , D 2 ) = ∑ k = 1 4 ω k q ( β | Ω k ), where q ( β | ω k ) is the posterior distribution for our parameter of interest from each configuration, β is the parameter of interest, and ω k is the posterior weight for the configuration. Each ω k in the MEM framework is estimated using Bayesian model averaging: ω k = P ( Ω k | D ) = π ( Ω k ) P ( D | Ω k ) ∑ j = 1 K π ( Ω j ) P ( D | Ω j ) . However, since there is no closed-form solution when considering regression models, [19] proposed a BIC to approximate this term so that ω k = P ( Ω k | D ) = π ( Ω k ) e x p ( − 0.5 Δ k ) ∑ j = 1 K π ( Ω j ) e x p ( − 0.5 Δ j ) , where Δ k = B I C k − m i n ( B I C 1 , B I C 2 , … B I C K ). In practice, we note that any other model selection criterion would also work.

Based on prior work by [16], we define a prior π e as a common probability for each supplementary data source being exchangeable with the primary data source, which is then used to estimate π ( Ω k ), the prior probability of a given configuration of exchangeability. Traditionally, π e can be obtained by calibrating until desired frequentist trial operating characteristics such as type I error rates or power are achieved. In our study, we utilized the value π e = 0.05 from [19], in place of fine tuned calibration of π e , to reduce the potential influence of supplemental data sources for a more conservative approach based on their reported operating characteristics. It is worth noting that while π e = 0.05 may seem overly conservative, [19] reported that it provided a good balance between increased power and bias.

While type I error rate and power are rooted as operating characteristics in the frequentist approach, Bayesian approaches often summarize these operating characteristics because they are requested per U.S. Food and Drug Administration guidance [10]. In this work, the High-Density Interval (HDI) for our Bayesian credible interval (CrI) is used to determine dose proportionality via equivalence testing. If the CrI is entirely contained within the equivalence limits, the dose is declared proportional. Specifically, we used the HDInterval package in R to estimate the HDI with arguments set to require only a single interval returned (i.e., if the HDI were multimodal the package returns the single interval with the highest density that covers the specified probability density) [20].

While numerous approach exist to group sequential designs, we choose a flat decision boundary similar to a Pocock boundary for all MEM approaches with interim monitoring to represent the same approach as proposed by [19]. This approach is implemented by estimating the Pocock boundaries from the gsDesign package and then estimating credible intervals adjusted based on the corresponding Z statistic from gsDesign for use in interim monitoring [1]. To avoid borrowing too much information from historical data when the primary sample size is small at the early stage of interim analysis, we also consider the constrained MEM proposed by [19] as a more conservative approach to borrowing as compared to the “unconstrained” MEM approach is used.

Our proposed method originates from the adaptation of MEM to simple linear regression as proposed by [19], applied in conjunction for parallel studies with observations assumed to be independent. This independence assumption, however, may not hold in the context of dose proportionality studies if a crossover design is employed where subjects are observed multiple times across different doses. Consequently, to account for the intra-subject correlations among observations, a linear mixed model (LMM) would be more appropriate. In this section, we propose an extension of MEM to LMMs, specifically tailored for crossover study applications.

In the primary and supplementary datasets considered in our methods, we assume every participant receives two doses, separated by a washout period following the initial dose assignment under the presumption of no carry-over effects. Let Y i j = l n ( C s s , i j ) denote the logarithmic transformation of C s s , i j , where i indexes the participants from 1 through n, and j represents the first and second observations. Assume that the jth observation for subject i, Y i j , is distributed as N ( β 0 + β 1 , σ u 2 + σ e 2 ). The covariance between the two observations of the same subject i, C o v ( Y i 1 , Y i 2 ), is assumed to be σ u 2 , and the covariance between observations of distinct subjects i and i ′ , C o v ( Y i j , Y i ′ j ), is assumed to be 0.

For illustration, we utilize a single supplementary resource, bearing in mind that this approach can readily be extended to encompass multiple supplementary resources. The linear mixed model for the non-exchangeability configuration (i.e., assuming the supplemental study is not exchangeable with the current study) is: (3.1) Y i j = β 0 + β 1 l n ( D o s e ) + β 2 I ( S = 1 ) + β 3 l n ( D o s e ) ∗ I ( S = 1 ) + u i + ϵ i j where S = 1 means the data is from the supplementary data. For the exchangeability configuration (i.e., assuming the supplemental source is exchangeable with the current study) is: (3.2) Y i j = β 0 + β 1 l n ( D o s e ) + β 2 I ( S = 1 ) + u i + ϵ i j where i = 1 , 2 , … , N; j = 1 , 2; u i ∼ N ( 0 , σ u 2 ); ϵ i j ∼ N ( 0 , σ e 2 ); σ u 2 and σ e 2 represent the variance of error introduced by different participants and observations, respectively;

To leverage the BIC approximation noted earlier, a set of models are fit using a frequentist approach which maximizes the restricted log-likelihood and then by the Bayesian approach using MCMC. From frequentist models, the BIC for the posterior weight calculation is easy to calculate. From the Bayesian models using MCMC, we have the following process to estimate β → = ( β 0 , β 1 , β 2 , β 3 ): 1.

Estimate the posterior distributions of β → = ( β 0 , β 1 , β 2 , β 3 ) from each exchangeable pattern. For example, with 1 supplementary source, there are 2 exchangeability patterns ( Ω 1 , Ω 2 ) each with its own separate regression model, and there will be 2 sets of β → from 2 different posterior distributions.

The outcomes are simulated from a log-normal distribution. We assume that data come from a cross-over study with no carry-over effects based on the design of the real-world trials motivating this work. For the primary study, each participant will be assigned multiple doses at a fixed interval until their plateau is reached. After a washout period, each participant will be given a new dose at a fixed interval until the plateau is reached again. However, not all of the participants will have two records, since if a study terminates early, some participants will only have one period of data. For supplementary data sources, all participants are treated with two doses, with a washout period after the first allocated dose assignment, again assuming no carry-over effects.

In data simulation, the standard error for all data sources is 0.15, which means that the unexplained variance between observations after controlling for dose and data sources is 0.0225. The standard error for observations from the same subject is 0.15, which means that the unexplained variance due to the difference between subjects after controlling for dose and data sources is 0.0225. The intercept is set at β 0 = 0 since it is not used to evaluate dose proportionality.

All considered scenarios are summarized in Table 1. We set the number of participants in the primary study as 36 and in the supplementary study as 48 to match the sample size in TFB-DP Data [29, 2]. Although large sample sizes are rare in phase 1 study, we still consider scenarios where the number of participants in the primary study as 100 and in the supplementary study as 200 to assess dose proportionality. Since dose level ranges from 25 to 100 and r = m a x / m i n = 4, 1 + l n ( 0.8 ) / l n ( 4 ) = 0.84 and 1 + l n ( 1.25 ) / l n ( 4 ) = 1.16. Those two values represent the boundary for defining proportionality, where our CI or CrI must be wholly contained between 0.84 and 1.16 to declare a proportional dose.

For the interim analysis, we only allow stopping for declaring dose proportionality. In other words, if the interim data show a CI or CrI within the (0.84, 1.16) interval, the study will be stopped early and dose proportionality declared. However, if any part of the CI or CrI falls outside of this interval, the study will continue enrolling until the next planned interim analysis.

Details of simulation settings are in the appendices. We also consider the simpler context where there are more traditional parallel arm PK dose studies instead of cross-over studies. The details are included in the appendices.

Three sets of models are applied across the different simulation scenarios. For correlated data, a mixed effect model takes the correlation into consideration (Full) and a linear regression ignores the correlation (IC). For uncorrelated data, linear regression is performed (NC). Three approaches are implemented for the simulation studies: Unconstrained MEM (MEM-U), Constrained MEM (MEM-C), and a traditional frequentist approach using a Pocock group sequential boundary (Pocock). We will mainly discuss the results from Full model, and the results from IC and NC will be discussed in the supplementary materials.

For the frequentist approach, REML is applied to obtain the estimated coefficients. For all Bayesian approaches, we set vague priors as 1 σ u 2 ∼ G a m m a ( 0.001 , 0.001 ) and 1 σ e 2 ∼ G a m m a ( 0.001 , 0.001 ). We also set the vague independent normal priors β ∼ N ( 0 , 100 2 ) on each regression coefficient. For the selection of π e we set the probability of any source being exchangeable equal to 0.05. As a sensitivity analysis, for select scenarios we also set π e to 0.01 and 0.001 to evaluate the sensitivity of results to source exchangeability prior specification. A total of 1000 simulations are conducted using R v4.2.0 (Vienna, Austria) [24] and RJags[22]

In Figure 1a, the bias of the Pocock approach is approximately 0 across all primary slopes for both smaller and larger sample sizes because no information is incorporated from the one supplementary source. The bias for MEM-C and MEM-U are approximately 0 either when the primary slope is equal to 1 and is exchangeable with the supplemental source or if the primary slope is equal to 1.5 and is different enough to be decidedly non-exchangeable. For both smaller and larger sample sizes, the most extreme biases of approximately ± 0.025 for MEM-U and ± 0.02 for MEM-C are observed for the 0.84, 0.95, 1.05, and 1.16 primary slope scenarios, pulling the primary slope estimate towards the supplemental source slope of 1. The bias attenuates towards 0 as the primary slope further departs from the dose proportionality slope of 1.

In Figure 1b, the MSE for the Pocock approach is approximately 0.002 across all primary slopes for the smaller sample size scenario and is approximately 0.001 for the larger sample size scenario. When the primary slope is 1, the MSE is approximately 30% lower for both MEM-C and MEM-U for the smaller sample size scenario and is 17% lower for MEM-C and 50% lower for MEM-U in the larger sample size scenario. When the primary source is exchangeable, this represents an area of improved efficiency.

The MSE is larger than the Pocock approach for almost all other scenarios due to the bias introduced when incorporating the non-exchangeable supplementary source, peaking at approximately 2 [3] times higher on the equivalence boundary for MEM-C and 2.75 [6] times for MEM-U in the smaller [larger] sample size scenario. However, when the primary slope is sufficiently different from the primary source at 1.5, MEM-C and MEM-U have the same MSE as the Pocock approach.

The probability of rejection to non-proportionality is the power under the scenarios of dose proportionality and is the type I error rate under the scenarios of non-proportionality. Figure 1c visualizes these results across different scenarios. When the primary slope is 1 for the smaller sample size scenario with 72 in the primary study and 96 in the supplemental study, the power for the Pocock approach is 78.6% compared to 98.0% for MEM-C and 98.2% for MEM-U. This increase in power of 20% with information sharing shows a potential strength of sharing information. In the larger sample size scenario with 200 and 400 in the primary and supplementary studies, respectively, all methods have 100% power.

In the small sample size scenarios where the primary source has a slope of 0.95 or 1.05, representing doses that may still be considered fairly proportional, the Pocock approach only has up to 56.4% power, compared to 88.0% for MEM-C and 89.0% for MEM-U. For the larger sample sizes, the MEM approaches have over 99% power compared to up to 97.5% for Pocock. These results indicate that in scenarios where you would still likely conclude a nearly proportional dose, information sharing improves power.

In contrast, information sharing does present a risk for inflated type I error rates. On the equivalence boundary of 0.84 or 1.16, Pocock’s type I error rate is up to 1.4% compared to 12.3% for MEM-C and 18.1% for MEM-U in the smaller sample size scenario. In the larger sample size scenario, Pocock’s type I error rate is up to 1.8% compared to 14.6% for MEM-C and 25.7% for MEM-U. However, the MEM’s type I error rates quickly decrease to more acceptable levels of up to 0.3% for MEM-C and 2.1% for MEM-U for primary slopes of 0.75 or 1.25, compare to 0% for Pocock in the small sample size scenario with similar results for the large sample size scenario.

In Figure 1d, the average stopping point for the simulation scenarios is depicted, where a value of 1/2/3/4 represents stopping at 25/50/75/100% of the expected trial enrollment. The only early stopping allowed was for early determination of dose proportionality.

In the smaller [larger] sample size scenario, for the (0.95, 1.0, 1.05) primary source slopes, the smallest average stopping rate was achieved for MEM-U at (2.7, 2.5, 2.7) [(1.5, 1.3, 1.5)], followed by MEM-C at (3.0, 2.8, 3.0) [(1.9, 1.7, 1.9)] and Pocock at (3.8, 3.6, 3.8) [(2.7, 2.4, 2.7)]. This represents a reduction of up to 31% [46%] for MEM-U and 22% [30%] for MEM-C in the smaller [larger] sample size scenarios relative to the Pocock approach which does not include information sharing.

In the smaller [larger] sample size scenario, for the (1.16, 1.25, 1.50) primary source slopes that represent non-proportionality are largest for the Pocock approach at approximately 4 for both smaller and larger sample size scenarios, indicating the method rarely stops early to incorrectly declare dose proportionality. In contrast, the average stopping point for MEM-U is (3.7, 3.9, 4.0) [(3.3, 3.9, 4.0)] and for MEM-C it is (3.9, 4.0, 4.0) [(3.7, 4.0, 4.0)]. These results suggest early stopping is more likely than for Pocock for the 1.16 and 1.25 slopes. Further, for larger sample sizes, the 1.16 boundary shows an even lower estimate for MEM-U and MEM-C compared to the smaller sample size scenario, suggesting that more information sharing may be present when the supplemental source is twice as large at 400 versus 200 (compared to 96 versus 72 for the smaller sample size scenario).

Given that the poor performance of MEM-C and MEM-U for the scenario when the primary slope is at the boundary of 0.84 and the supplementary slope is at 1 with π e = 0.05, we further investigated the behavior of MEMs under this scenario at different prior source exchangeability weights of π e = 0.01 and π e = 0.001 to see if we can decrease the bias, MSE, and type I error rate at the boundary while still maintaining the power. Figure 2 presents how operating characteristics changed as the weights decreased.

As the weight for primary data increases from 0.95 to 0.99 and to 0.999 (i.e., π e decreases from 0.05 to 0.001), the bias and MSE all decreased, and the average stopping points are increased. The type I error rate decreased to 0.05 for the small sample size, while power is still maintained above 0.9. However, the type I error rate is still elevated around 0.08 in the large sample size scenario for MEMs. MEM-C has generally better balanced performance than MEM-U since it has a lower bias, MSE, and type I error rate, while still having reasonable power. In addition, as the weight for primary data goes up, the lines from the MEM-U converges to MEM-C.