Journal of Biopharmaceutical Statistics
`
`ISSN: 1054-3406 (Print) 1520-5711 (Online) Journal homepage: http://www.tandfonline.com/loi/lbps20
`
`Dose response studies I. some design
`considerations
`
`Stephen J. Ruberg Ph.D.
`
`To cite this article: Stephen J. Ruberg Ph.D. (1995) Dose response studies I.
`some design considerations, Journal of Biopharmaceutical Statistics, 5:1, 1-14, DOI:
`10.1080/10543409508835096
`To link to this article: https://doi.org/10.1080/10543409508835096
`
`Published online: 29 Mar 2007.
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`ATI 1018-0001
`
`ATI v. ICOS
`IPR2018-01183
`
`

`

`journal ot Biopharnraceutrcal Sata\tm, 5 i j , i - i i , l r r S ,
`
`Ke:,, void.^. Dmg development; Factorial studies; Minimum effec-
`tive dose; One-sided tests; Randomized concentration controlled trials
`
`A critical aspect of biomedical research is the characterimtion of
`response reiationship el' a c~rnpmind. This is iriiii iii lab-
`the
`oratory experiments and clinical triais and pertains to efficacy, safety,
`-. , . .
`resuifing brnrili,/r~~$. ratill. fiesen:i,ii, here is Pzrt I (;[
`;hi:;
`2nd
`article, which deals with some ciinical trial design issues surrc)unci-
`ing dose response studies. Some additional comments are made about
`trials for identifying the minimum effective dose, randomized con-
`centration controlled trials, and the use of one-sided hypotheses in
`6esigr.i~g suck! trials. Part I1 is a separate paper reviewing some
`zn~lysis srr&egie.: f ~ r <.!out- i-esponw sti.ii:ies.
`
`Understanding the dose response relationship of a compound is a fundamental
`aspect of research; indeed, it may bc the central issue. This is true whether
`studying a new drug, assessing the effect of environn~ental toxins, or eval-
`
`Copjr~ght C 1995 by Marcel Dehker. Inc
`
`ATI 1018-0002
`
`

`

`2. Some Experimental Designs
`
`2.1 Parallel Designs
`
`The most ronmon and straightforward design is the placebo-controlled, ran-
`domized, parailel dvse response study. In this siiliiji design, patients are ran-
`domly ailocated to one of several active dose groups or placebo. This design
`is nost p ~ p u j a r since the ~ n i y diffcr~ncx ictwccn xrcrrrment groups i:;
`the
`dose of the experimental compound, aiiowing for straightforward interpre-
`tation of the results of such a trial. it is also imporiant that the study inciude
`a placebo group since a significant trend in response with iqcreasing dose in
`the absence of placebo is not necessarily evidence of a drug effect (Fig. 1).
`
`ATI 1018-0003
`
`

`

`Dose Response Smdies, i
`
`c-.-
`
`Us-
`
`In Figure 1 , if the placebo response were absent, onc might conclude there
`.
`. .
`dose effect because respcmse is increasing with dose. How-
`Is a .;lonif~canf
`-IblLa,;,,g
`ever, when the "trendB in psponsc .#ith irn.--
`is taken ir, light of
`$OX
`the placebo response, it may be doubtful that there is any drug effect.
`There are some exceptions to this principle of needing a placebo group
`to assess the significance of dose respozse. Ir, s ~ m e cases, the historical rL nia-
`cebo response is nil or nearly nil (e.g., spontaneous cures of serious infections
`. .
`such 2s efidecar-ilis, the absence of nailsea and vc-,mi:ing fs!!owir,g highly
`emetogenic chemotherapy, or chronic asthma), and therefore, a concurrent
`placebo group is not necessary. Furthermore, ti-om a safety staidpoint, there
`may be instances where a single serious adverse event is evidence of a toxic
`drug effect in the absence of placebo.
`.
`.
`Ill
`instances,
`like to use dose t;trat;on to assess the dFdG b
`effect. This is appealing early in drug development programs since patient
`safety is generally of greater concern. in these trials patients can 'bc started
`at low doses, and depending on their response, doses can be increased grad-
`uailj: tc: achieve a suitable dnse f ~ r
`the patient. The al;ses;men[ :,f ai: in&-
`vidua! p&ient's dose response is satisfying ciinicaiiy and may require fewer
`patients to assess the drug effect since within-patient variability is used.
`The disadvantage of titration studies is that dose and time effects cannot be
`completely separated. Since efficacy and adverse events may have a time-
`
`ATI 1018-0004
`
`

`

`m
`
`The disadvantage of a parallel dose response trial is that the precision of the
`ii:fsrence is driver, by between-subject variabi!ity, which usaa!ly requires greater
`sample sizes to increase the precision of the estimates for drug effect. To
`overcome this ilifficulty, crossover trials can be ~atilizcd so that within-subject
`variability, which is most after, sma!!es
`than between-snl?ject variability, car?
`5e used in the infereccc. Thc statistical criteria for when 2 crossover design
`is better than a parallel design, as well as practical considerations (e.g., the
`stab;iiry =f :he disease state c.x,rer time) are well knuwr! (2). lhrrp I r e several
`variations of the crossover study, but two fundamental designs are the com-
`- , , - A ~ - ; , ~ A
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`
`Typically, Latin squares are used for completely randomized crossover
`studies. When a very broad dose range is of interest, the use of incompieee
`crossover studies (Youden squares or balanced incomplete block designs) can
`be employed effectively. In many clinica! settings it is not possible to evaluate
`clifiical endpoints in a short period of time or ;vithout se-e carric\x:p,r
`J - . " . effect.
`However, in c!inical pharmacology studies where surrogate endpoints of ef-
`-LLy f Lirc , used in the decision-making process ol drug deveioprnenr,
`C- licacy or
`such conditions may hoici. Furthermore, pharmacokineiic dose proportivri-
`" - < .--- L; ,-?-,., :1:.1-:1'
`: O I : ~ I U I ' L I V ~ ~ X : C C I I ; I I ~ u . ~ a v i l i : a u l i ~ i ~ studies ofieri have many
`aii-iy ;ti?c&eh o r ' .--.-I.-':
`treatments or doxc groups. Such studies are weii suited to the use of Youden
`squares ur variaiicins on balanced incompkte block designs. 'if there is a con-
`trol group or reference formulation that serves as a control, optimal blocks
`designs for comparisons with control have been developed (3).
`
`ATI 1018-0005
`
`

`

`cludie~ arc !ncrewing ifi popularity 2s resr,arcfiers
`Factorial d r . ~ e Icsmnw
`I -
`recognize the importance of studying two factors simultaneously to find op-
`timai dosage regimens. There are several different factorial dose rzsponse
`studies that are very useful in drug development.
`- A of study considers the magnitude of the dose and the frequency
`One type
`of dvse as the two factors of inkrest (Design 2). As seen in that design, there
`is need for only one placebo regimen, which is usua!!y covered by r'hc zero
`dose for the most frequent regimen of interest, in this case BID dosing. This
`design is most usehill in mid-to-late phase I1 ciinica! development ir? order to
`find an optimal regimen for phase 111 studies. This type of design might also
`
`Period
`
`Design I . Dose escalation crossover study
`
`ATI 1018-0006
`
`

`

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`
`the placebo group and on the highest dose-by-fi.equency regimen to get a
`more powerful test of the drug effect, Of course, this assumes that the greatest
`dose amount produces the largest difference in response from placebo.
`Another variation on this type of design is with intravenous !i.v.) drugs
`where nne f a c t ~ r is the i.v. bolus dose that may be given as initia! them PI T r
`and the ~ t h e r factor is the i.v. infusien rate used for maintenance therapy
`(Design 3). In this case one can study a placebo for both bolus and infusion
`rates, thereby giving ar, independent assessment of pure dose response h r
`
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`
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`Design 3. Optimizing i.v dose regimen. Generally. use equal sample sizes in each cell
`
`ATI 1018-0007
`
`

`

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`S:3tir;ticians have lone - recogrll~rd
`the advantages of using fact~riai ex-
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`jimii]taiico.i;sly. TI-aditicnaliy, clinicims hive heen reluctant to use iac-
`.
`torial studies becausc h e y require a iargcr saiiipic sizz, o: for a fixed sample
`
`size, there are fewer observations ai each dose regimen. Obi~i~fi~ij.., the ie-
`quirernent for larger sample size in such studies is needed because several
`hypotheses are being evaluated within the same design. 4 s mentioned earlier,
`nne can intentionailv irnbaiance the design and oversanipie the placebo group
`2nd a high-dme group to iiicrcase the c h a x c s of having a statistical!y Q ~ O -
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`Design 4. Optimi~ing combination therapy. Generally, ute equal sample sizes in each cell.
`
`ATI 1018-0008
`
`

`

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`cacious and wouid provide a wider safety margin. In fact, the FDA has made
`a formai assessment of dosage changes and reports that approximately 10%
`of drugs (new molecular entities) that were approved in 1980- iY8Y have had
`dosage changes (mostly decreases in dosej of greater than 33% ((6. There
`has also been some recent controversy sumunding the drug Ha!cjon@, am!
`in one statement, the European Community's Con~inittee for Proprietary Me-
` the lowest effective dose should
`dicinal Products JCPMPj has suggested, " . .
`.
` . " (7). Finally, with the lilcreased crriphasis on switching drucrc 6"
`be used .
`.
`to OTC status, Carl Peck, formerly of the FDA, has suggested that one of
`. -
`the fundamental questiGas that needs t= be ar,sxvr;eied for O'rC s.r~;t-h
`w ILLII ~ a u -
`*.',-
`didates is "what is the MED?" (8). While this principle of determining the
`MED is easily stated, it is very hard to define in practice and has both an
`efficacy and a safety compcnent.
`I would like to propose the following definition of the MED. The MED
`is ;Ize s;;zaj/est dGse pf.oducing
`c/i;;icGi/y inzlpoi-tcxnt re
`ti'lat i?an be
`declared statistically; ,sigi?$ficantly &,fir-r.n<frnrn the plircebo respmse. Therc
`needs to be a clinicaiiy lmgortant response because small, statis~icaily sig-
`nificant responses can be meaningless. There needs to be a statistically sig-
`nificant response since large, clinical responses that are nut clearly distin-
`guishable from placebo response do not provide substantive evidence of dmg
`effectiveness.
`When doing a study to assess the MED, a placebo group is essential for
`the reasons given previously. Since many dose response studies have iden-
`
`ATI 1018-0009
`
`

`

`Dose Response Studies. ?
`
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`The choice oi sample size in dose response srudies is a difflcdi issue.
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`I ; i ~ ~ l i i x i iii2~0rla11~ ques;!~:; !s hox&
`i:,istribule the <:;Epic Size ::~IOSX :f:r
`dnsc grmrps. Of course. this is cioseiy rieci to the anaiysis strategy for ir-'-'-,-
`'ranulg
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`paiirl>is in rbi.
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`. A!lhcmgh H 3 1 ~ may be il good idea for piikwise comparise;.ns,
`cimtsrd - g,r~?~?p.
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`ilc;fiti~;ist tests ( 1 ~ jc discc:,hej jiil_:!e ;g rsgt 11;
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`6 9 s ~ ranee being
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`extrcmeq of
`Piiii-j~ ,,,,; numbers of patients wor-~lil be a!lncated to the
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` while intermediate-dose groups or
`placebo group and the high-dnse group,
`regimens would aii have snialler but equal numbers of patients a!!ccated.
`There is no simple answer to the sample size al!ocatlon problem. One
`must carefully define thc objectives of the study and the primary test of in-
`terest
`then coinpuie p o ~ e i - f o ~ various al&-nativc hypotheses sr,d sar*l,p!e
`size configurations in order to obtain the bcst study design. In some instances
`simulations may be required when power calculations cannot be easily done
`for more complicated analysis strategies. An analysis strategy rhac maximizes
`the minimum power against a variety of likely or suspected alternative hy-
`potheses is generally most desirable.
`An alternative design to the randomized parallel dose response study for
`assessing the MED is the following. One couid randomize patients in doubie-
`blind fashion to drug or placebo. Patients are given a supply of medication
`with instructions to take, for example, " 1-2 tablets, once or twice a day."
`-
`number of
`ratients wouid they! tilratt; themselves by taking the
`tzbiers over rbe course of the day to cmtrol their symptoms. One could es-
`timate the MEU by assessing the average daily dose consiimed by the patients
`during the study. Furthermore, if the response to drug was significantiy dif-
`ferznt from placebo, then .me coilld claim xhar this estimated MED is j i g -
`nificantly different than placebo, thereby satisfying the criteria for an ade-
`qmte, well-controlled trial. Of course, this study design is usefui oniy when
`the disease or symptoms can be evaluated by the patient (e.g., pain, allergy).
`It also is appealing in that it mimics real life situations since patients often
`
`ATI 1018-0010
`
`

`

`*
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`the trial and adjusting thi dose as necessary to maintain the cijncciitraiion
`ing
`range. This is motivated by the fact that individual pharmacokineeics may
`play a large roie in assessing the drug effect. That is, individuais randomized
`to a fixed dose may exhibit widely differing responses due to widely differing
`pharmacokinetics. Those who respond may absorb the drug more completely
`or eliminate it more slowly, thereby producing higher blood levels of the
`drug. Those who do not respond may 'naive lower 'niooci ievels Gom rapid
`elimination or incomplete absorption. This has intuitive appeal since dose
`response trials are based on how much drug is ingested (i.e., gets into the
`gut), whereas concentration controlled trials are based on how much drug is
`circulating ifi the b!=o&trea,vk. &es~r;,ab',~, provides a better meta~,eter
`for drug efficacy since what is circulating in the bloodstream is likely to be
`closer to the site of action than what is ingested into the gut.
`Such studies may be useful for drugs that have a direct or immediate
`effect on an easily measured endpoint (e.g., blood pressure). They could be
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`p i n t (e. g . , congestive heart failure, Alzheimer's disease). Another diffi-
`culty in randomized concentration controlled trials is that using the drug con-
`centration in plasma as a metameter for assessing drug effect may induce
`more variability into the analysis than using dose. If concentrations are mon-
`itmed periodically throughout a trial and doses adjusted accordingiy, there is
`a tremendous reliance on that single blood level as an accurate measure of
`the patient's exposure to the drug. In fact, that concentration may be driven
`by the very recent dosing history of the patient (i.e., the time of the last dose
`
`ATI 1018-0011
`
`

`

`Dose Response Studies. 1
`
`a c s %
`
`ed Versus Two-Sided Hypothesis Testing
`
`-C n n a c;riori x r e r r i i c t \ x i n - ~ i A ~ T i h\innihPYiY i r \ i ; r l u ~e
`__I-___a --,elxlS i(T1 De One
`TL- t--;-
`l l l C LUplL U l ullb-aluvu v v ~ v u u r r , u uA u v u yV---il-l
`of those statistical issues that draw strong opinions from both sides. While
`the issue is relevant for aii phases of drug deveiopmeni, it seems of panicular
`relevance in designing and analyzing dose response trials. The topic is in-
`cluded here since the issue really starts with the design of the trial and the
`Ir,suriltlr " j;iitiplb jiii; i i ; y t i l i i L , . v i i L J The analysis then f n l l o ~ s nzt~rl!!y from
`-:-- ..l\-...lrYmPnt"
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`the design of the trial and the scientific hypothesis of interest. A series of
`articles from this Journd by distinguished authors give a comprehensive re-
`vie\;r/ of this issue ( l l- 15). There is very little to add to their arguments, bui
`the salient points wi!I be summarized here.
`With the exception of Dubey, all authors favor the use of one-sided
`hypotheses for comparing experimental therapies versus placebo. As a gen-
`eral rule, the authors who favor one-tailed hypotheses justifiably base their
`argument on the fact that the most important error to control is Pr (drug
`
`ATI 1018-0012
`
`

`

`an incredibly conservative control of the false positive error rate. This con-
`scwatism comes at quite a price. By switching to me-tailed hypctheses at e
`= .05 instead of two-tailed hypotheses, approximately 25% fewer patients
`could be utilized. Since much of the clinical development costs are driven
`by the number of patients (number ~f case report, farms; z m o g ~ t sf
`o
`suppiics; number of invesf gators; number of personnel to nmnitor trials, build,
`clean, analyze, and report on the data), and clinical development costs are
`typically tens of millions of dollars jscmerimes hundreds ~f miiiions of dol-
`lars!), the potential savings are enormous! There is also a tremendous poten-
`A . 1 "-- '
`~ i a l baviiigs in the development time f ~ r ne\i; drugs, ctmcntly 7-!G jicars. I t
`should be noted that the cost and time savings are not the ends that justify
`the means, but rather a beneficial outcome of taking the appropriate scientific
`approach.
`Finally, several of the authors discuss the significance level of hypoth-
`esis tests that is appropriate when &siEning studies. Next; drugs that are fidr
`-
`-
`-
`non-life-threatening diseases or that represent an incremental improvement
`over existing therapies require two trials demonstrating a significant dnig ef-
`fect at the a = .05 ievei from one-railed tests. New drugs for Me-fhreatening
`diseases or serious diseases for which no good therapies exist generally need
`only one trial demonstrating drug effectiveness. Fisher (13) notes that in these
`circumstances, perhaps a = .a25 for a one-taiied test is appropriate. if the
`drug has been approved for other similar indications or is in a class of drugs
`for which the biological understanding is firm, then Fisher suggests using a
`
`ATI 1018-0013
`
`

`

`References
`
`Rcjddn BE, Tsianco M r . bolognese 1.4, Kerstcn MK: Ci~nicai de~ielupmeni. in: Sio-
`i7hrtrmnce~~tical Stii?isiic.~,for Dncg Deveioptnenl (Peace K E , Ed). Marczl Cckker. N w
`York, 1988.
`Fisher AC, Wa!ienstei~? S: Crossover designs in medical research, In: Stntistics in the
`Pharmaceutical Industry (Buncher CK. Tsay JV, Eds). Marcel Dekker, New York,
`. ,-%%-p
`,
`I Y n l .
`Hedayat AS, Jacroux M, Majurndar D: Optimai designs for comparing test treatments
`with controls, Statist Sci, 3:462-491, 1988.
`Peace KE, Koch GG: Statistical methods for a three-period crossover design in which
`high dose cannot be used first. J Eiophurm Stntisr 3: 103- 1 16, 1993.
`Stablein DM, Novak JW, Peace KE, Laska EM, Meisner MJ: Optimization in clinical
`tria!r: and combination drug development. In: Strrlisriral issurs in Drug i2esearch and
`Development (Peace K E , Ed.). Marcei Dekker, Xew 'ioi,k, 1886.
`Fiiil: Reports, Thc pi& shee::. 53(i8): 14- i5, ?./lay 6 , 1991
`FDC Reports, The pink sheets, 53(42):9-10, Oct 21, 1991.
`F!X Reports, The p ~ n k \hcers. 5315j:T&Gi5-7&Gi6, r e b 4, i991.
`Dwnetr 3CW: .4 rnuitipic comparison procedure for comparing several treatments with
`a conirol. Anz Srutist Assoc J 50: lij96- i i 2 i . 1955.
`Sana~hanar, LP, Peck CC: Thc randomized concentratien-controiied trial An evaiuaiion
`of its sampie site efficieiicj;. Controlled C!in T,rials !2:780-794,
`!991
`Peace KE: One-sided or two-sided p values: Which most appropriately address the ques-
`tion of drug efficacy'? J Biophurm Stccrist 1 : 133-138, 1991.
`
`ATI 1018-0014
`
`

`

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`SCi: St;.me thoughts 39 the oIle-sided and [.,:o-:;ded
`h i h e y
`1:13.3-;50, 1.991,
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`rnrmhrr'j p e ~ c c y t i i ' e . J P.ludza.r:x St~?l.i.f 1 : 15 I - 156. 1 9'3 !
`. . - -. - - -
`,
`14. Overall JE: A comment concerning one-sided tests of significance in new dnig appli-
`<c;iricm:: J Biq>Jicir,vi S r ~ r i s ~ 1 . 157.. 160~ lg9 1
`Sfitfir: i : 61 - -e.
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`ATI 1018-0015
`
`