7
The Choice of Treatments
aIn line with the terminology introduced in section 2.4, in this chapter we shall use the term “experimental treatment” when referring to the main object of a clinical trial (often a novel treatment), and the term “study treatments” when referring to both experimental and control treatments.
In a clinical study, in addition to the study treatments, there may also be con- comitant treatments. Both categories of treatments must be described in detail in the research protocol.
7.1. Study Treatments
Experimental treatments are the intervention of interest that one wants to study in a given disease or condition. As discussed previously, they are evalu- ated in comparison to other treatments, called control treatments. The experi- mental and control treatments constitute the study treatments, to be distin- guished from the concomitant treatments. The latter can be taken during the study, but are not the object of the experimentation.
As mentioned in chapter 1, the experimental treatment can be of different types, as summarized below.
• Pharmacological, for example, a novel inhibitor of cyclo-oxygenase isoen- zyme-2 (COX2 inhibitor) against arthritis pain.
• Surgical, for example, a new form of partial gastrectomy (that is, partial removal of the stomach) against multiple or recurrent gastric ulcers.
• Psychotherapeutic/behavioral, for example, a specific form of psychotherapy against anxiety.
• Logistical/organizational, for example, normal hospital wards instead of intensive care units for selected patients with myocardial infarction.
The general principles of clinical research methodology are identical, what- ever the nature of the experimental treatment, even if some procedural, logis- tical and ethical aspects may differ. Unfortunately, the experience of the authors of this book is limited to pharmacological treatments. Therefore this book is inevitably unbalanced towards such treatments. However, we want to stress that in non-pharmacological therapeutic areas the need for rigorously performed clinical experimentation is equally great, but there are relatively few researchers capable of applying the general principles of research methodolo- gy to their respective disciplines.
Control treatments should represent the state of the art therapy for the con- dition under study at the time the trial is performed. If no treatment of proven efficacy and/or acceptable safety/tolerability exists, the control treatment should be a placebo. A placebo can be defined as an inactive treatment, iden- tical to the experimental treatment in every aspect, except for the presumed active ingredient(s) or intervention. The placebo is used as a control treatment with the aim of separating the intrinsic effect of the experimental treatment from other effects, often more powerful, linked not to the treatment itself, but to the process of treating the patient, including the expectations, psychological influences, nursing support, duration of hospitalization, etc. To this end, it is very useful that the study treatments be administered in a blinded (or masked) fashion, that is, such that neither the patient nor the research staff know which study treatment is administered to which patient. The method- ological reasons and practical implications of the use of placebo and of the blinding of study treatments will be discussed in depth in chapter 9.
If the experimental treatment is a capsule, the matching blinded placebo will also be a capsule, as close as possible to the former in shape, size, color, appear- ance, flavor and smell. If the experimental treatment is a partial gastrectomy for multiple and recurrent ulcer, the corresponding blinded placebo (at least in theory) would be a surgical intervention with the same anesthetic procedures, skin incision, duration, suture and post-surgical procedures, but without the actual gastrectomy (it is obvious that there are ethical problems here - see below). In a study evaluating the efficacy of a given form of psychotherapy for treating anxiety, the blinded placebo would be a set of “mock” psychotherapy sessions identical in context and duration to the “real” ones, but in which the psychologist administers to the patients a generic form of support instead of the specific psychotherapy under study. Finally, when logistical measures are evaluated, the blinded placebo can be obtained by standardizing the logistical context in which the study is conducted. In the above mentioned example, comparing the efficacy of intensive care to that of traditional hospital stay, the patients assigned to the latter may be placed in the intensive care ward, but receive a normal level of care (i.e. with all of the bedside monitors turned on but not used), so that neither the patients nor their relatives realize that the care level administered is really that of a “normal” hospital ward.
As with many other topics in this book, it is not possible to cover the topic of placebo to the extent it would deserve. All we will do here is to briefly address some of the issues resulting from the use of this methodological artifice.
The use of a placebo in a clinical study causes many ethical problems. First of all, the basic question arises as to whether the use of placebo is in itself ever ethical: is it ethically acceptable to administer a treatment we know to be inac- tive? Furthermore, even admitting that the practice as such is acceptable, is it ethical to use a placebo that involves invasive procedures, such as the sham gastrectomy operation mentioned above? Many articles have been written on this topic, in support of very diverse positions. In our opinion, in the great majority of cases, the use of a placebo as a control treatment is more than acceptable ethically, it is an ethical imperative, whenever the available treat- ments (which may be used as controls in the study) have not been conclusive- ly proven as safe and effective in methodologically sound confirmatory studies.
The only exception may be that of advanced stages of serious diseases, charac- terized by very poor quality of life, almost no chance of remission, and/or very short life expectancy (in other words, situations unlikely to be worsened by the hypothetical toxicity of a non-effective treatment). Many forms of terminal cancers belong to this category. The patient may unfortunately have little to lose, but it must be the patient him/herself, or his/her guardian, to decide this, not the researcher! In such cases, the most ethical behavior is probably to accept the risks of the experimental treatment and administer it to the whole study sample in the hope that it will show some efficacy. However, we want to emphasize that the conditions belonging to this category are few. Even for dis- eases with fatal outcome, if the quality of life is reasonably good (for example because not in an advanced stage), the use of the placebo is recommended in the absence of an active control of proven efficacy. From these short com- ments, it is evident that in extreme situations the choice concerning the use of a placebo is very subjective and may be quite dramatic (as are many other med- ical choices in such situations) and there are no easy rules. In any case, the will of the patient (or guardian if the patient is incapable of understanding the sit- uation and expressing his/her will) is paramount: it must be actively solicited through an appropriate explanation of the problem, and must be respected.
The ethical implications of the use of a placebo reach well beyond the basic principle. Even those who consider ethically acceptable the use of placebo, as we do, justify its use only in the absence of an active treatment of document- ed and adequate efficacy and safety. The problem is that there is no consensus on the clinical value of many treatments commonly used in clinical practice. For example, inhaled corticosteroids in the treatment of chronic obstructive pul- monary disease (COPD) are considered efficacious by many specialists and largely used in clinical practice. However, various studies and authoritative experts consider the continuous use of these drugs in COPD ineffective, if not harmful. Is the use of placebo as the control treatment justified in a study eval- uating a new drug in COPD? To complicate matters further, many regulatory authorities including the FDA in the United States, typically impose the use of
a placebo in confirmatory clinical trials, even in diseases for which the majori- ty of experts in the scientific community agree that an active treatment of ade- quate efficacy and safety does exist.
The issues concerning the use of placebo are not only ethical, but also methodological and practical.
• There are situations where a placebo matching the experimental treatment to ensure blinding is either impossible to make or not compatible with the objectives of the study. For example, if one wants to evaluate the impact on quality of life of a given therapeutic regimen (as opposed to the efficacy of the pharmacological principle), one needs to compare the experimental treatment regimen (e.g. once a day) to a control treatment regimen (e.g.
twice a day), which is not compatible with the use of a placebo.
• The manufacturing of a placebo requires considerable technical and econom- ical resources. Underestimating the complexity of this process is a dangerous mistake that can delay the start of the study by many months.
Returning to the choice of the study treatments, numerous are the decisions the researcher must make and describe in detail in the protocol before starting the study. The most important ones are summarized in sections from 7.1.1 to 7.1.4.
7.1.1. How Many Treatments
It is intuitive that the more study treatments one wants to compare in the same clinical trial, the more complex the trial will be. As the number of study treat- ments increases, so do the many other aspects of the study: the number of patients, the methodological and statistical complexity of multiple compar- isons, the logistical complexity of the production, blinding, packaging and dis- tribution of the treatments, the amount of data generated and the consequent complexity of data management (see section 2.2. for a discussion of the conse- quences of an excessive complexity of the study). Among the many ways in which a study can become excessively complex, the ambition of evaluating many treatments in the same study is one of the most common. There is no general rule concerning the acceptable number of experimental and control treatments in the same trial. In dose-response studies, where the study drug is administered as single dose or for short periods of time and the end-points are instrumental measurements, a relatively high number of treatments can be fea- sible. The statistical analysis of these trials may benefit from numerous treat- ment arms, if based on regression techniques, comparing the trends of the dose-response curves (see [86]). Conversely, for studies with treatments of long duration, end-points based on clinical outcomes or measurements (which typically require large sample sizes), and objectives of confirmatory nature, that is aimed at deciding on the best treatment among those being compared, it is generally dangerous in our experience to go beyond three, maximum four, treatments per study, whatever the experimental design (see also [85]).
7.1.2. What Treatments
In addition to choosing how many treatments one wishes to study, it is also necessary to choose which ones to study (it is obvious that in practice, these two aspects are not sequential, but concurrent). One or more experimental treatments will naturally be among the study treatments. The choice of dose(s) and frequency of administration of an experimental treatment is all but easy, especially in the early stages of the clinical development process. Clearly, in dose-response studies more than one dose will be chosen. But which ones?
What should the lowest dose be? What should the highest one be? How many intermediate doses? Based on what criteria should the doses be chosen?
Sometimes, even in phase III, more than one dose of the experimental treat- ment is tested (this occurs, for example, when phase II studies were not able to fully define the profile of two adjacent doses). The frequency of administration often determines the success of a drug on the market. Among the leukotriene antagonists, a relatively new class of drugs used in the treatment of asthma, the once daily montelukast has been more successful than other drugs of the same class that reached the market earlier, such as pranlukast, as the latter must be administered three or four times a day. Unfortunately, pharmacokinetic data alone are not always sufficient to predict the optimal frequency of administra- tion of a drug; therefore, it can be very useful to test more than one dosing reg- imen before starting large phase III studies.
If the choices concerning the experimental treatment are not easy, those con- cerning the comparator treatment or treatments are often even more complex.
We have already discussed the placebo. When it comes to active controls (or comparators), it is a matter of choosing a treatment of proven efficacy (and adequate safety) that is considered the “standard of care”. The problem is that often many different treatments are used in clinical practice, with numerous national and even regional differences in preference. For example, the thera- peutic armamentarium for hypertension offers many classes of widely used drugs (beta-blockers, diuretics, ACE inhibitors, angiotensin II inhibitors, etc.), each class including many drugs of common use. Antihistamines are frequent- ly used in the treatment of bronchial asthma in Japan, but are hardly used in this condition in Europe and the United States. To make things even more com- plex, fixed combinations of drugs, often very commonly used in clinical prac- tice, add to the list of available options (e.g. the fixed association of diuretic and ACE inhibitors in hypertension, or of β2-agonist and corticosteroid in asthma).
And this is not all: in many therapeutic areas, including the above mentioned hypertension and bronchial asthma, the pharmacological treatments can be integrated with (or substituted by) dietetic treatments and physical therapies, not to mention the so-called complementary treatments, such as massage, homeopathic agents, etc. What should a researcher wishing to test a novel anti- hypertensive or antiasthmatics treatment compare it to, given the methodolog- ical and practical limitations described above? As always, the final choice will be a mixture of considerations of scientific, regulatory, practical and commer- cial nature, combined with personal preference.
From a methodological point of view, it is important to decide from the very beginning if the objective of the trial is to establish the superiority or non-infe- riority of the experimental treatment compared to the active control. For non- inferiority studies, the choice of the control drug (including its dose and dosing regimen) is even more critical than for superiority studies (see ICH guideline [61]). In fact, in a superiority study, a statistically and clinically significant result favoring the experimental treatment can be taken as evidence of effica- cy, even if the active control has an uncertain efficacy or is not used at its opti- mal dosage. It is obvious, however, that for the purpose of concluding “real superiority” of the experimental treatment over the active control, it is essen- tial that the latter be administered with the optimal dose and dosing regimen (see ICH guideline [62]). On the other hand, in a non-inferiority study, a posi- tive result leads to the conclusion that the experimental treatment and the active control are both efficacious. This conclusion will be all together wrong if the control is not truly active, because intrinsically ineffective or because it has been given at the wrong dose and/or with the wrong regimen. Even though it is a common belief that experiments with active controls have less ethical prob- lems than those with placebo (because all patients receive an “active” treat- ment), this is not always true. It should not be forgotten that patients receiving the experimental treatment do not receive the standard therapy of proven effi- cacy (at least in the parallel group designs - see chapter 10).
Regulatory and practical concerns may well be the ones that prevail in the end. For example, if a study is conducted for registration, that is, its goal is to provide confirmatory evidence for the regulatory authorities to approve a new treatment, it will often be necessary (or highly advisable) to follow specific guidelines providing essential information on how to design such studies [62].
As mentioned above, placebo very often appears in registration studies for this very reason. Sometimes the regulatory guidelines also indicate what treatment is to be used as active control. From a practical point of view, if one intends to blind the study treatments (see below), it is useful to choose an active com- parator that is easy to manufacture (if not protected by a patent) or to modify into a “blinded” galenical form (see below).
Finally, sometimes commercial considerations have great importance, since the pharmaceutical company sponsoring the study can, depending on the study, “strongly recommend” or “strongly discourage” the selection of specific treatments as active comparisons. For example, remaining in the field of hyper- tension, an article in the Journal of the American Medical Association (JAMA) has recently been published on results of a clinical trial comparing a diuretic, a calcium channel blocker, and an angiotensin converting enzyme (ACE) inhibitor [1]. The conclusion of this study was that diuretics have an effect very similar to that of the other two treatments in reducing the incidence of coro- nary heart disease and of other cardiovascular diseases. Considering these data, and in light of the fact that diuretics are very cheap and generally well tolerat- ed, one would think that a company developing a new treatment for hyperten- sion should plan at least one clinical study with a diuretic as the active control.
In fact, most likely, if such a study were to succeed in demonstrating the supe- riority of the new treatment over diuretics, its results would be “valuable” in supporting a premium price of the new treatment once it reaches the market.
Sometimes commercial rationales like the one mentioned are legitimate, but at other times they are not. The researcher must be able to make his/her own mind up and must have the strength to refuse to collaborate with companies that force (or deny) the choice of active controls (as well as of other key aspects of the experimental design), based on reasons that in his/her opinion are not legitimate.
To conclude this section, the so-called “add-on” studies deserve mention.
The classic design of this type of study has two treatment groups: the experi- mental treatment group receives the new treatment in combination with the standard treatment (which can itself be a combination of several treatments), while the control group receives only the standard treatment. Therefore, the experimental treatment is “added-on” to the standard treatment. In this partic- ular case, the experimental treatment is the combination of the new treatment and the standard therapy, since in this experiment one can only verify the effi- cacy and safety of the combination. To establish the efficacy of the new treat- ment alone it is necessary to administer it in mono-therapy to patients in a third treatment group.
7.1.3. Blinding of the Study Treatments
Having chosen the number and nature of the study treatments, we are only half way done. At this point we need to decide whether or not we want to “blind”
them and, if so, the level of blinding desired. Blinding is a very important aspect of the methodology of clinical research, both conceptually, as an instrument for avoiding some very frequent forms of bias, and practically, for the challenge of pharmaceutical development and manufacturing of blinded treatments. Section 9.3 is dedicated to a more detailed discussion of these issues, while here we will only remind the reader that the manufacturing of blinded placebos and active controls can require many months and, if underestimated, can delay the start of the study. It is not rare that the company responsible for the production of blinded placebos and active controls requires more than one year of advance notice before delivery.
7.1.4. Packaging and Logistics
Once the study treatments are obtained, they must be properly packaged. Each package will contain the study treatment for a single patient. Sometimes it will also contain one or more concomitant treatments, such as rescue medications (see below) or drugs used as background therapy in add-on studies (see sec- tion 7.1.2).
In some cases, it is possible to include the entire treatment destined to a sin-
gle patient in one “patient pack” and prepare all of the patient packs from the same production batch. However, in many other cases this is not possible. The reason for this is that all pharmacological and dietary treatments (including placebos) have expiration dates, after which they cannot be used. Therefore, in studies with long enrolment and/or long treatment duration, one or more study or concomitant treatments may expire before the projected end of the trial.
This implies a very complex process of staggered packaging, which must take into account the expiration date of each of the study treatments, as well as that of the concomitant treatments, if packaged together with the study treatments, the duration of enrolment of the study subjects, and the length of the treat- ment.
Furthermore, an “adequate” label must be attached to each patient pack. The labeling of the patient pack, far from being a simple administrative act, is an important, complicated and treacherous process, for several reasons, not least because it is full of legal implications. The label must contain many types of information. First, it must be identified by a unique identification code (numer- ical or alphanumerical). In randomized clinical trials, this code is the only link between the treatment contained in the pack and the randomization list.
Consequently, mistakes in coding the labels generate confusion over the assign- ment of treatments. A mistake of this type (or even the suspicion that one has occurred) can destroy the credibility of a study, to the point of preventing its use for registration purposes. The process of randomization was introduced in chapter 2 and will be discussed in depth in chapter 9. In non randomized stud- ies, the code in the label will coincide with the treatment number assigned sequentially to each treated patient (note that the treatment number may be different from the enrolment number since some patients who enter the screening process may never receive the study treatment for a variety of rea- sons).
In addition to the randomization code (or the treatment number for non-ran- domized studies), the labels must contain a considerable amount of informa- tion, including the medication batch number, the country of production, the expiration date, a warning that the content of the pack is (or may be) an exper- imental treatment. Some of this information is required by law in the country in which the study is performed, and must be in the local language. When multi- center studies are performed in multiple countries, another level of logistical complexity is added: an accurate estimate of the number of patients to be enrolled in each participating country is needed, since, once the patient packs have been delivered, it will not be easy to transfer them from one country to another. Multilingual labels sometimes represent a partial solution to this prob- lem.
Finally, the patient packs, properly labeled, must be shipped to the study centers. Once again, this process conceals numerous risks. Many drugs require special couriers to avoid breakage and/or to ensure proper transport conditions (for example, refrigeration). In some countries, there are long waits at customs (sometimes for “quarantines” imposed by local laws, other times for inefficien-
cy and slowness). More than once we have had treatments become unusable due to problems occurring in this final stage.
In clinical studies, there are many other issues related to the production and logistics of the study treatments, so many, in fact, that we cannot even begin to mention them here. However, we hope that through this short overview we managed to give an idea of the complexity of the process, which requires high- ly qualified specialists who are an integral part of the research staff. The expe- rienced clinical researcher will always have a special regard for the advice from colleagues in charge of treatment logistics, because often they will be the first to realize the excessive complexity of the study. For trials conducted as collab- orations between a pharmaceutical company and the clinical centers, it is gen- erally the industry that is responsible for treatment logistics (entire depart- ments are dedicated to these tasks). For trials performed independently from industry, we recommend that the issue of treatment logistics be addressed in the very beginning of the planning process. If the study is carried out in one or few centers, sometimes an experienced pharmacy of one of the participating centers can take responsibility for this task. However, in most cases, we strong- ly recommend that treatment logistics be delegated to a company specializing in this area.
7.2. Concomitant Treatments
Concomitant treatments are all the treatments allowed during the study without being the object of the experimentation. For example, if in a study aim- ing to evaluate the pain killing effect of a novel COX2 inhibitor in rheumatoid arthritis, the patient takes an aspirin for a headache (adverse event), aspirin represents a concomitant treatment. Concomitant treatments are not neces- sarily pharmacological. For example, physiotherapy for headache caused by cervical spine problems, if allowed during a study, would be a non-pharmaco- logical concomitant treatment.
It is not possible to exclude with certainty the possibility of a concomitant treatment interfering with the desired and/or undesired effects of one or more of the study treatments. In some cases, these interferences are completely unpredictable; in other cases they can be predicted or at least suspected on the basis of the mechanisms of action of the concomitant and study treatments. In the above example, we know that aspirin can influence both the efficacy and the safety/tolerability profile of COX2 inhibitors. Aspirin will positively affect efficacy, as it is proven to be efficacious against pain in rheumatoid arthritis, in addition to being active against headache. Vice versa, safety and tolerability will be negatively influenced, since aspirin damages the gastric mucosa, with con- sequences ranging from gastritis to ulcer to hemorrhage. Such a negative effect is especially damaging in the context of our example, since the class of COX2 inhibitors has been specifically developed to reduce the gastric side-effects of the other non-steroidal anti-inflammatory drugs (including aspirin).
Therefore, it is clear that the use of concomitant treatments must be careful- ly regulated by the protocol of a clinical study. This does not mean the solution is simplistically that of prohibiting all concomitant treatments. This approach (which unfortunately we see with some frequency) is almost never useful. Even in the early studies on healthy volunteers (phase I), the complete elimination of all concomitant treatments dramatically reduces the number of subjects that can be enrolled in a study and the number of subjects completing the study without violating the protocol.
Generalizing, the earlier the phase of the clinical development of an experi- mental treatment, the more restrictive one must be concerning concomitant treatments, since it is necessary to assess the “intrinsic” efficacy (or activity) and tolerability of the new treatment at an early stage. However, in our view, even in these early phases it is appropriate to make concessions for some com- monly used concomitant treatments, unless there are obvious reasons to sus- pect interactions with the study treatments. Pain killers, oral contraceptives and vaccines can be included in the category of concomitant treatments for which a concession should be considered even in the early phases of clinical development.
When one reaches the stage of large, phase III pivotal studies, in our opinion, it is very important to be as liberal as possible with concomitant treatments. If we are evaluating a corticosteroid in COPD, as in one of the previous examples, we know that the population under study will have a large proportion of sub- jects who are elderly and suffering from cardiovascular diseases (cigarette smoking predisposes to both COPD and cardiovascular conditions). What value would there be in evaluating the efficacy and safety/tolerability of the experi- mental treatment when all of the drugs used in the therapy of angina, heart fail- ure, arrhythmias, etc. are excluded? Naturally, if there is a reason to believe that specific concomitant treatments may worsen the side effects of the exper- imental treatment or reduce its benefits, these must be excluded also from phase III studies. However, the researcher must be aware of the consequences of such an exclusion, which will necessarily translate into a contraindication or warning in the “package insert” once the experimental treatment eventually reaches the market. If the excluded concomitant treatment is truly important, special studies aimed at investigating potential interactions at the pharmacoki- netic, pharmacodynamic and therapeutic level will need to be planned.
In practice, some level of restriction on concomitant treatments must also be applied in phase III studies. In the post-registration phase (the so-called phase IV), these restrictions can be eliminated for the most part.
Finally, it should be noted that concomitant treatments can be used as mark- ers of the efficacy and/or tolerability of the study treatments. For example, the efficacy of a new COX2 inhibitor in the treatment of pain from tooth extraction can be evaluated by measuring the time between the extraction and the first
“rescue” intake of a pain killer or by counting the number of rescue doses taken in the first six or twelve hours after the operation. Likewise, the efficacy of an inhaled corticosteroid in the COPD can be evaluated by calculating the mean
number of daily inhalations of rescue albuterol (also known as salbutamol, a reliever of shortness of breath with fast onset and short duration of action) over a sufficiently long period of time (1-3 months). The intake of concomitant treat- ments functions well as an end-point in many therapeutic areas, since it is clearly linked to the level of control of the disease under study and is general- ly easy to quantify.
Summary
In a clinical trial one should carefully define both the study treatments, i.e. the experimental and control treatments, and the concomitant treatments. The experimental treatments are the main objects of the experimentation and are evaluated in comparison with the control treatments. The experimental and control treatments, which include the placebo (an inactive treatment, identical to the experimental treatment in every aspect except for the presumed active substance), as a whole, constitute the study treatments. The concomitant treat- ments are drugs or other forms of treatment that are allowed during the study, but are not the object of experimentation. For each type of treatment, the researcher must make many choices, from the selection of the treatments, to their mode of administration, to the method of blinding the experimental and control treatments. These choices must be described in detail in the study pro- tocol, as most of them directly influence both the conduct and analysis of the study.
