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Crossover designs are well-known to have major advantages when comparing the effects of various non-curative treatments. We compare efficiencies of several crossover designs along with the Balaam’s design with that of a parallel group design pertaining to longitudinal studies where event time can only be measured in discrete time intervals. With equally sized sequences, the parallel group design results in the greater efficiency if the number of time periods is small. However, the crossover and Balaam’s designs tend to be more efficient as the study duration increases. The degree to which these designs add efficiency depends on the baseline hazard function and effect size. Additionally, we incorporate different cost considerations at the subject level when comparing the designs to determine the most cost-efficient design. Researchers might consider the crossover or Balaam’s design more efficient if the duration of the study is long enough, especially if the costs of applying the baseline treatment are higher.

A well-known type of outcome in longitudinal studies is the survival endpoint with the research interest focused on the occurrence and timing of some events. The timing of events can be measured continuously using thin precise time units (e.g. minutes or days). Under some circumstances, however, it is far less feasible to measure the timing of events this precisely. Instead, it is measured discretely using a set of discrete intervals like years, months or weeks. Here, an event might occur at any point in time during an interval but is only measured once at the end of each interval until event occurrence, drop-out or the end of the trial. Since the time of event occurrence is rounded upward to the nearest measure- ment time point, a loss of information will occur if the exact time is unknown. Data with this type of survival endpoints are called discrete-time survival data as opposed to data recorded on a continuous scale, i.e. continuous-time survival data.

It is useful to measure time discretely in retrospective studies where subjects can only supply event times in ranges or round numbers due to memory failure. In a suicide ideation study, for instance, subjects may not remember the exact day of their first suicidal thought, but may remember how old they were at the time. Discrete-time survival data are also encountered in prospective studies where it may not be feasible or practical to follow subjects continuously. In a smoking initiation study, for example, researchers are not able to contact sub- jects every day to record the onset of smoking, but may do so on a regular basis, say once a month. Another reason for measuring event occurrence in discrete time is if events can only occur at a few points in time, e.g. a student can graduate from college on a few occasions in the academic year.

Optimal designs and statistical power analysis have been important tools in designing longitudinal studies with a variety of types of outcomes. For trials with discrete-time survival outcomes, [

Crossover designs are powerful designs in bioequivalence, clinical and pharma- ceutical trials if the disease is chronic and treatments have a reversible or non- curative effect. The major advantage of crossover over parallel group designs is that crossover designs eliminate part of the inter-subject variability from the treatment comparisons, and thus might require fewer subjects to provide the same level of power. For a discussion on the analysis of crossover designs with continuous and binary outcomes, see [

Crossover designs have rarely been applied with right-censored survival data [

The aim here is to determine whether and if so, to what extent, a crossover design is more efficient than a parallel group design with discrete-time survival outcomes if subjects are not further observed after experiencing the event. An example of a crossover design with discrete-time survival endpoints is a fertility study was conducted to study the effect of ovarian stimulation on increasing the chance of conception [

We consider the most common AB/BA crossover design where subjects switch to the other treatment after one time period. For practical purposes, other variations of this design are also considered such as the AABB/BBAA design where subjects alternate the treatments after multiple time periods or appli- cations of a given treatment. The efficiency of these designs are also compared with that of the Balaam’s design [

The organization of this paper is as follows. In the next section, an overview of the logistic regression model for analysing discrete-time survival data is pre- sented; see [

We consider designs with two treatments A and B, and s sequences of treat-

ments. Let N = ∑ s k = 1 n k be the total number of subjects in the design, with n k

the number of subjects randomly assigned to sequence k at baseline. The underlying continuous event times are recorded in discrete time intervals indexed by j = 1 , 2 , ⋯ , p . These intervals represent a series of consecutive periods in continuous time with equidistant cut points t 0 = 0 , t 1 = 1 , ⋯ , t p = p . The baseline measure is taken at time t 0 = 0 , just before randomization, and the total duration of the follow-up of a study with p periods ends at time t p = p . Note that t 0 = 0 is the “beginning of time” when no one has experienced the event yet but everyone is eligible to do so. The first measurement of event occurrence is taken at time point t 1 , and any event occurring after t 0 and before t 1 is classified as happening during the first time interval [ t 0 , t 1 ) . The j th time interval [ t j − 1 , t j ) ( j = 2 , 3 , ⋯ , p ) begins immediately at time point t j − 1 and ends just before time t j .

The binary response Y i j k for subject i ( i = 1 , 2 , ⋯ , n k ) in period

j ( j = 1 , 2 , ⋯ , p ) receiving sequence k ( k = 1 , 2 , ⋯ , s ) is measured once at the end of each time interval and defined according to whether the subject ex- periences the event of interest ( Y i j k = 1 ) or not ( Y i j k = 0 ) . The expected value and variance of Y i j k are E ( Y i j k ) = h d [ j , k ] ( t j ) and var ( Y i j k ) = h d [ j , k ] ( t j ) [ 1 − h d [ j , k ] ( t j ) ] where h d [ j , k ] ( t j ) is the discrete-time ha- zard probability that the subject experiences the event in period j under treatment d [ j , k ] . It is given by h d [ j , k ] ( t j ) = Pr ( Y i j k = 1 | Y i j ′ k = 0 for j ′ < j ) . It is the conditional probability that an event occurs in interval j under sequence k for subject i given that the event has not yet occurred before period j . Note that d [ j , k ] = A or B denotes the treatment used for subject i in period j under sequence k . Note that repeated measurements per subject are con- sidered to be conditionally independent.

The discrete-time hazard probability h d [ j , k ] ( t j ) for subject i assigned to se- quence k in period j is modeled as:

logit h d [ j , k ] ( t j ) = log h d [ j , k ] ( t j ) 1 − h d [ j , k ] ( t j ) = ∑ j = 1 p α j D i j k + β Z i j k , (1)

with the time-dependent explanatory variable Z i j k denoting the treatment con- dition and Z i j k = 1 if the subject receives treatment B, and = 0 otherwise. For a given time period, the parameter β denotes the effect of treatment B relative to treatment A on the probability of event occurrence on the logit scale,

so β = log h B ( t j ) / [ 1 − h B ( t j ) ] h A ( t j ) / [ 1 − h A ( t j ) ] . As can be seen, the parameter β is constant

across time. We assume that model (1) is a proportional odds model. The dummy variable D i j k is set to 1 in time interval j and 0 elsewhere. The corresponding intercept parameter α j is the value of the logit hazard pro- bability corresponding to treatment A in that particular time period so

α j = log h A ( t j ) [ 1 − h A ( t j ) ] for j = 1 , 2 , ⋯ , p .

Model (1) can be formulated in matrix form as:

logit h ( t ) = X θ ,

where the vector h ( t ) contains discrete-time hazard probabilities of event occurrence for all p time periods and all N subjects until they experience the event or leave the study before event occurrence or the study concludes (i.e., if j = p ). The parameter vector θ = ( α 1 , α 2 , ⋯ , α p , β ) ′ is a column vector of ( p + 1 ) unknown parameters. The design matrix X is of order

∑ s k = 1 ∑ p j = 1 n j k × ( p + 1 ) , with n j k representing the number of subjects in the k th

sequence entering the j th period and leave the study neither due to event occurrence nor unforeseen reasons prior to time period j . The total number of subjects at the beginning of the study in sequence k is n 1 k = n k , and the total number of subjects entering period j ≥ 2 is

n j k = n ( j − 1 ) k [ 1 − h ^ d [ j − 1 , k ] ( t j − 1 ) ] [ 1 − r k ( t j − 1 ) ] = n k S ^ d [ j − 1 , k ] ( t j − 1 ) ∏ h = 1 j − 1 [ 1 − r k ( t h ) ] .

Here, p is the estimate of the discrete-time hazard probability, and N is the estimate of the probability of the subject will experience the event after time > 60 . The notation δ = 0.05 refers to the treatment in the pre- ceding period, i.e. the δ th time period. It can be concluded that the risk of event occurrence in period h A depends on the survival probability then and in the previous period using h d [ j , k ] ( t j ) = [ S d [ j , k ] ( t j − 1 ) − S d [ j , k ] ( t j ) ] / S d [ j , k ] ( t j − 1 ) . What is more, the attrition rate r k ( t h ) denotes the proportion of subjects in sequence k who leaves the study during time period h due to reasons other than event occurrence. In this study, we assume a constant attrition rate across all the time periods and treatment sequences, i.e. r k ( t h ) = r for any h ∈ { 1 , 2 , ⋯ , p } and k ∈ { 1 , 2 , ⋯ , s } . We assume non-informative attrition (i.e. missing at ran- dom), that is the non-censored subjects do not differ systematically from the censored subjects. This means those who remain in the study are representative of everyone who would have remained in the study had there been no censoring.

The common method for estimating the vector of unknown parameters θ is iteratively re-weighted least squares [

Cov ( θ ^ ) ^ = [ ∑ k = 1 s ∑ j = 1 p X ′ j k w ^ d [ j , k ] ( t j ) X j k n j k ] − 1 . (2)

The vector X j k corresponds to subjects in the j th time interval in the k th sequence, and has ( p + 1 ) elements with value 1 on the j th element, value 0 or 1 on the ( p + 1 ) th element, and 0 elsewhere. So the first p elements re- present the values on the dummies D 1 , D 2 , ⋯ , D p , and the ( p + 1 ) th element re- presents the value of Z j k . The scalar w ^ d [ j , k ] ( t j ) is the least squares weight for subjects in period j under sequence k . For a logit link function, it is given as w ^ d [ j , k ] ( t j ) = h ^ d [ j , k ] ( t j ) [ 1 − h ^ d [ j , k ] ( t j ) ] . It should be noted that the ( p + 1 , p + 1 ) th entry of Cov ( θ ^ ) ^ is proportional to the variance of the estimator of the treatment difference (i.e., β ) and it will be used for the definition of the optimal designs.

We consider trials with a maximum duration of p max = 12 time periods where subjects may be observed over p = 1 , 2 , ⋯ , or p max time periods. So p max is the maximum number of time periods a trial can be conducted in and p is the number of time periods at hand. Note that the larger p is, the longer the duration of the follow-up. For easy comparison of the hazard probabilities in each period, we assume the time points are equally spaced and the distance be- tween any pair of adjacent time points is fixed in advance. Under this assumption, the duration of a trial with p max = 12 time periods is twice as long as the du- ration of a trial with p = 6 time periods.

The first design is the parallel group (PG) design where subjects are randomly assigned to sequences with a single treatment A or B. The other three designs are crossover (CO) designs where subjects receive treatments A and B according to a pre-established order during the study, but switch to a different treatment after one or more multiple periods of using a given treatment. In the CO1 design, subjects use the two treatments sequentially for fixed periods of time, and switch to treatment A or B after one time period. In the CO3 design, subjects alternate the use of the two treatments after three applications of a given treatment so the switching time point is three. The PG and CO designs are based on two treat- ment sequences in which some part of the subjects are randomly assigned to the first sequence and the remaining subjects to the second sequence. The last design is the Balaam’s (BM) design, a four-treatment-sequences design that assigns some parts of the subjects to the (AB/BA) sequence and the remainder to the (AA/BB) sequence. This design may be considered a combination of the PG and CO1 designs. It should be noted that we compare the designs of equal total duration or follow-up time ( p ) and sample size at baseline ( N ) .

We study the efficiency of the PG design compared with that of an alternative design to determine which design estimates the parameter β more efficiently.

Design | Sequence | Period | |||||||||||
---|---|---|---|---|---|---|---|---|---|---|---|---|---|

1 | 2 | 3 | 4 | 5 | 6 | 7 | 8 | 9 | 10 | 11 | 12 | ||

PG | 1 | A | A | A | A | A | A | A | A | A | A | A | A |

2 | B | B | B | B | B | B | B | B | B | B | B | B | |

CO1 | 1 | A | B | A | B | A | B | A | B | A | B | A | B |

2 | B | A | B | A | B | A | B | A | B | A | B | A | |

CO3 | 1 | A | A | A | B | B | B | A | A | A | B | B | B |

2 | B | B | B | A | A | A | B | B | B | A | A | A | |

CO6 | 1 | A | A | A | A | A | A | B | B | B | B | B | B |

2 | B | B | B | B | B | B | A | A | A | A | A | A | |

BM | 1 | A | B | A | B | A | B | A | B | A | B | A | B |

2 | B | A | B | A | B | A | B | A | B | A | B | A | |

3 | A | A | A | A | A | A | A | A | A | A | A | A | |

4 | B | B | B | B | B | B | B | B | B | B | B | B |

To do so, we consider the PG design as the reference design and compare the performance of the other designs using the relative efficiency (RE):

RE CO | PG = var PG ( β ^ ) var CO ( β ^ ) , RE BM | PG = var PG ( β ^ ) var BM ( β ^ ) .

If RE CO | PG = 1 , the CO design is as efficient as the PG design. If RE CO | PG < 1 , the PG design is more efficient, and if RE CO | PG > 1 , the PG design is less efficient than the CO design. In addition, the RE CO | PG − 1 indicates how many subjects should be taken under the CO design to be as efficient as the PG design [

We assume the probability of event occurrence for treatment A does not vary across the time intervals, so h A ( t j ) = h A for j = 1 , 2 , ⋯ , p . Since finding a closed-form formula for the variance-covariance matrix in (2) is complicated, the results are presented for selected choices of h A and the difference between the probabilities of treatments A and B ( δ = h B − h A ) . We study the efficiency and cost efficiency of a PG design in comparison to three alternative CO designs, namely CO1, CO3, and CO6, along with the BM design.

groups. Each group in the PG and CO designs contains N 2 subjects and in the BM design, each group contains N 4 subjects.

As can be seen in

design more often tends to become more efficient than the PG design for a larger p than the CO designs.

We observe almost similar results if a constant attrition rate r is taken into account. The only difference is that the REs approach unity more gradually as p increases if 5 % or 10 % of the subjects are lost to follow-up in each period within each sequence, implying that the CO and BM designs require more time periods to be equal or more efficient than the PG design (results not shown).

We now look for the time point when the CO1 and BM designs are as efficient as the PG design. We have p ˜ denote the smallest number of time points when RE CO1 | PG > 1 or RE BM | PG > 1 . For computational and practical reasons, we limit our search to sixty periods.

Previous section shows a pair-wise comparison of efficiency of the designs for studies with 1 to 12 time periods. In such a comparison, we did not make a distinction between the costs of sampling subjects and the costs of treating and measuring them. However, if recruiting a subject costs differently than taking measurements from that subject and the cost of treating this subject with treatment A is different than that with treatment B, we should account for the cost differential when we compare the five types of the designs. To this end, we take two cost functions as a function of the number of time periods for each type of the designs into account. Let c 0 represent the initial cost for setting up a study. If c 1 denotes the cost to include a subject in the study, let the cost of taking one measurement be denoted by c 2 . If c A denotes the cost to treat a subject with treatment A, c B denotes the cost to treat a subject with treatment B. Cost function I is then computed for a study with p time periods, s

Study designs | r = 0.00 | r = 0.05 | |||||
---|---|---|---|---|---|---|---|

BM | 22 | 17 | 11 | 28 | 20 | 12 | |

BM | 12 | 10 | 7 | 13 | 10 | 7 | |

BM | 5 | 4 | 3 | 5 | 5 | 4 | |

CO1 | >60 | >60 | >60 | >60 | >60 | >60 | |

CO1 | 37 | 48 | >60 | >60 | >60 | >60 | |

CO1 | 13 | 11 | 9 | 17 | 14 | 10 |

treatment sequences, and N subjects at baseline as follows:

C − c 0 = N c 1 + N c 2 ∑ k = 1 s ∑ j = 0 p S d [ j , k ] ( t j ) + N 2 ∑ k = 1 s ∑ j = 0 p − 1 c d [ j , k ] S d [ j , k ] ( t j ) . (3)

With this cost function, we assume that subjects leave the study once they have experienced the event and measurements are not taken after event occurrence. S d [ j , k ] ( t j ) is the survival function for the treatment d [ j , k ] under sequence k by the end of time period j and t 0 = 0 is the baseline. Therefore, the number of measurements (including one baseline measurement) for each subject in sequence k is given by 1 + ∑ j = 1 p S d [ j , k ] ( t j ) . Note that subjects are treated by treatment d [ j , k ] = A or B at the beginning of each time period, and so the number of treatment applications for a subject in sequence k is 1 + ∑ j = 1 p − 1 S d [ j , k ] ( t j ) .

If it is assumed that subjects leave the study after experiencing the event or due to reasons other than event occurrence, the number of measures for each subject is given by 1 + ∑ j = 1 p S d [ j , k ] ( t j ) ( 1 − r ) j . Cost function II can then be represented as follows:

C − c 0 = N c 1 + N c 2 ∑ k = 1 s ∑ j = 0 p S d [ j , k ] ( t j ) ( 1 − r ) j + N 2 ∑ k = 1 s ∑ j = 0 p − 1 c d [ j , k ] S d [ j , k ] ( t j ) ( 1 − r ) j .

To determine the most cost-efficient design for a given number of time periods, we normalize the optimality criterion (i.e. var ( β ^ ) ) by multiplying it by the cost C − c 0 . In other words, we compare the designs based on:

RE CO | PG = var PG ( β ^ ) var CO ( β ^ ) × C PG − c 0 C CO − c 0 , RE BM | PG = var PG ( β ^ ) var BM ( β ^ ) × C PG − c 0 C BM − c 0 .

In this case, var ( β ^ ) under each design is penalised by the amount of costs of that design which accounts for the number of time periods and for different costs of treatment A and B. We compare the designs for different combinations of the costs at the subject-level (i.e. c 1 , c A and c B ). The costs at the measure- ment level is fixed to c 2 = 1 .

more efficient choice when treating subjects costs more than recruiting the subjects and also when treatment A is less costly than treatment B (i.e. c 1 < c A < c B ). The efficiency of the other alternative designs, however, tend to increase as p becomes larger so that the BM design becomes more efficient than the PG for p ∈ { 5 , 6 , ⋯ , 12 } when h A = δ = 0.2 . The CO designs, on the other hand, need to be conducted for a longer time to become more efficient than the PG design; the CO1 and CO3 designs become more efficient for p ≥ 9 when h A = δ = 0.2 . When all the subject-level costs are equal (i.e. c 1 = c A = c B ), the efficiencies of the CO designs and the BM design is very close to that of the PG design, and the efficiency of these designs tend more often to exceed unity as h A and δ become larger. In the last scenario, when sampling subjects is less costly than treating subjects and the cost of treatment B is lower relative to the cost of treatment A, the CO and BM designs are most often more efficient than the PG design. In this case, the CO and BM designs are always preferable. Overall, we observed very similar results to those of

Up until now we have focused on equal allocation proportions for each of the treatment sequences of the designs. From a clinical or ethical point of view, there might be reasons for an unequal assignment of subjects. For the BM design, for example, it might be considered unethical to give subjects the same treatment multiple times if its efficacy is unknown [

the BM design randomly allocates π N 2 to the (AB/BA) sequence. We now

compare the designs efficiency as a function of π for a given p . We limit our search to π ∈ [ 0.25 , 0.75 ] and assume that the treatment sequences contain at least a quarter of the subjects.

We first focus on the results for c 1 < c A < c B which implies treatment B is more costly than treatment A. When h A = δ = 0.05 , the REs of the CO designs are larger than unity if π is small; the designs are almost equally efficient if π ∈ [ 0.40 , 0.45 ] , and the PG design is more efficient than the CO designs as π increases further. If h A and δ increase to 0.2, the REs of the CO designs become closer to that of the PG design which implies the effect of π becomes smaller and thus a negligible gain in efficiency from any CO or PG design is obtained. As can be seen, the RE line of the BM design has almost a similar ∪ - shape. This makes sense since the BM design is a compromised design between the CO1 and the PG designs when π = 0.5 . For a smaller π , the BM design allocates more subjects to the sequences of the PG design and therefore its efficiency is in favor of the efficiency of the PG design for a small π . Similarly, the BM design allocates more subjects to the sequences of the CO1 design for a large π and therefore its efficiency is in favor of the efficiency of the CO1 in this case. So the BM design tends to be more efficient than the PG design as the sequence sizes become more unequal.

As treatment B becomes as expensive as or less expensive than treatment A (i.e. c 1 = c A = c B or c 1 < c B < c A ), a higher efficiency is most often maintained by the CO designs compared to the PG design as π becomes larger, especially if h A = δ = 0.2 . In this case, it is seen that the BM design becomes even more efficient among all the designs as π increases.

In the introduction, an example of a CO design with right-censored survival

outcomes is given by a study investigating the effect of using controlled ovarian hyper-stimulation on the probability of conception via intrauterine insemination (IUI) [

We use the rates in the ovarian stimulation cycles as the probability of con- ception in each cycle for the current treatment. We presume there is a newly developed treatment expected to further improve the efficacy of IUI in in- creasing the probability of conception, and the difference between the two treat- ments on the logit scale is β = 0.5 .

Allocation proportion | Subject-level costs | Study designs | |||
---|---|---|---|---|---|

CO1 | CO2 | CO3 | BM | ||

1.02 | 1.01 | 1.04 | 1.58 | ||

1.15 | 1.09 | 1.14 | 1.84 | ||

0.89 | 0.92 | 0.94 | 1.33 | ||

0.99 | 0.99 | 0.99 | 1.00 | ||

0.97 | 0.97 | 0.97 | 0.99 | ||

1.02 | 1.02 | 1.02 | 1.01 | ||

0.98 | 0.98 | 0.96 | 1.53 | ||

0.82 | 0.87 | 0.82 | 1.26 | ||

1.15 | 1.11 | 1.08 | 1.81 |

design for different allocation proportions and three combinations of costs at the subject-level. In the first combination, we assume sampling couples to be as expensive as treating them with either treatment. For the other combinations, we assume that stimulated cycles cost differently than those in which IUI is applied with the new treatment. We observe that if π = 0.5 , all the designs are almost equally efficient since the REs are either very close or equal to 1; researchers can then choose the design that best counters the practical objections, regardless of design cost. If π = 0.2 , the CO designs are almost as efficient as the PG design when both treatments cost equally (i.e. c A = c B ), or they become more efficient when offering IUI in a new treatment cycle is more expensive than in cycles with ovarian stimulation (i.e. c A < c B ). The reverse happens if π = 0.8 , meaning that the CO designs are less efficient when c B ≥ c A . With unequal treatment sequences, the BM design is always a more efficient choice among the designs. However, the RE of this design depends on design cost when π ≠ 0.5 .

The present study is designed to compare the efficiency and cost efficiency of the crossover (CO) design and Balaam’s (BM) design with that of a parallel group (PG) design in trials with discrete-time survival endpoints. We consider designs with two treatments A and B and focus on how efficient a design is for estimating differences between the treatment conditions. We consider CO designs that di- ffer in the number of time periods after which subjects switch to the other treat- ment. All the calculations are performed in R and our R syntax is available upon request from the first author.

Using this efficiency comparison, our study shows that the efficiency of esti- mating treatment differences can be increased by a proper choice of the design. Deciding on whether the CO and BM designs are more efficient than the PG design depends on the size of true treatment differences ( δ ) , the baseline hazard probability ( h A ) , and on the study duration ( p ) . This depends also on whether or not the efficiency comparison is penalized by the amount of costs that a design has and whether or not attrition is taken into account. In general, we find that if the treatment sequences are equally sized, the CO and BM designs are less efficient than the PG design if p is small, and a larger gain in efficiency may be obtained using the CO or BM designs instead of the PG design if p is larger. The effect of a prolonged study duration on the efficiency of the CO and BM designs is larger if δ and h A are larger. We also observe that the BM design requires fewer time periods than the CO designs to become as efficient as the PG design. The CO and BM designs are either as efficient as or more efficient than the PG design when treatment B costs less or the same as treatment A. In cases where the baseline treatment is more expensive, the PG design is most often more efficient. In addition, all the designs perform almost equally well if the treatment sequences are of almost equal sizes for a given number of time periods. In studies with unequal allocation proportions, the BM design is preferable.

A similar comparison between a CO design and a PG design can be seen in the work of [

In the current study, we confine our focus to a model where the subject effects are fixed. However, if a design is efficient under the fixed effect model, it will also perform well under the random subject model [

In conclusion, the possible advantages of a CO design compared to those of a PG design have been previously addressed in longitudinal studies with a variety of outcomes including the survival outcome. A similar investigation of the discrete- time survival data where the event time can only be measured on a discrete scale instead of a continuous scale has yet to be conducted. Our study provides addi- tional findings on the usefulness of the CO and BM designs over the PG design if the treatment effect, baseline hazard function and number of time periods are varied.

This research was funded by a VIDI grant from the Netherlands Organization for Scientific Research (NWO) number 452-08-004.

Safarkhani, M. and Moerbeek, M. (2017) A Comparison of Wi- thin-Subjects and Between-Subjects Designs in Studies with Discrete-Time Survival Outcomes. Open Journal of Statistics, 7, 305- 322. https://doi.org/10.4236/ojs.2017.72023