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Efficacy of azole therapy for tegumentary leishmaniasis: A systematic review and meta-analysis
research-article
Publication date (Electronic):
9 October 2017
Journal:
PLoS ONE
Publisher:
Public Library of Science
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Abstract
Background
Several controlled and uncontrolled studies addressing azole antifungal drugs for cutaneous and mucosal leishmaniasis have been published with inconclusive results. We conducted a systematic literature review of studies evaluating the efficacy and toxicity associated with azole therapy for tegumentary leishmaniasis.
Methodology
PRISMA guidelines for systematic reviews and the Cochrane manual were followed, and the review methodology was registered (PROSPERO; CRD42016048668). Sources included the EMBASE, Web of Science, MEDLINE, LILACS, and IBECS databases along with a manual search of references from evaluated studies. Additional resources such as Google Scholar and clinicaltrials.gov were also searched. We included all studies reporting cure rate after cutaneous or mucosal leishmaniasis treatment with systemic azole drugs, regardless of their design. R software was used to estimate global rates of success and adverse events with each drug. The main outcome of interest was clinical cure, defined as complete re-epithelialization of all lesions.
Results
A total of 37 studies involving 1259 patients that reported outcomes after fluconazole (9), ketoconazole (14) and itraconazole (15) treatments were included. Only 14 (38%) were randomized controlled trials (RCT). The pooled azole final efficacy rate was 64% (CI95%: 57–70%) for all studies and 60% (CI95%: 50–70%) (p = 0.41) if only RCTs studies were considered. Twenty-four studies were conducted in the Old World and 13 studies in the Americas. The final efficacy rate according to New and Old World were 62% (CI95%: 43–77%) and 66% (CI95%: 58–73%), respectively. The final efficacy rate of azoles according to species were 89% (CI95%: 50–98%) for L. mexicana; 88% for L. infantum (CI95%: 27–99%); 80% for L. donovani; 53% (CI95%: 29–76%) for L. major; 49% for L. braziliensis (CI95%: 21–78%); and 15% (CI95%: 1–84%) for L. tropica. The cure rates were similar among the fluconazole, ketoconazole and itraconazole group arms (p = 0.89), specifically 61% (CI95%: 48–72%), 64% (CI95%: 44–80%) 65% (CI95%: 56–72%), respectively. Adverse events during fluconazole, itraconazole and ketoconazole therapy were reported in 7% (CI95%: 3–14%), 12% (CI95% 8–19%) and 13% (CI95%: 6–29%) of treated patients, respectively, without difference among them (p = 0.35). This systematic review included studies with small samples and both non-comparative and non-randomized studies and the main limitation was the low quality of the available studies.
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Most cited references60
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The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomised trials.
Michael Altman, Thomas K F Schulz, D Moher … (2001)
To comprehend the results of a randomised controlled trial (RCT), readers must understand its design, conduct, analysis, and interpretation. That goal can be achieved only through total transparency from authors. Despite several decades of educational efforts, the reporting of RCTs needs improvement. Investigators and editors developed the original CONSORT (Consolidated Standards of Reporting Trials) statement to help authors improve reporting by use of a checklist and flow diagram. The revised CONSORT statement presented here incorporates new evidence and addresses some criticisms of the original statement. The checklist items pertain to the content of the Title, Abstract, Introduction, Methods, Results, and Discussion. The revised checklist includes 22 items selected because empirical evidence indicates that not reporting this information is associated with biased estimates of treatment effect, or because the information is essential to judge the reliability or relevance of the findings. We intended the flow diagram to depict the passage of participants through an RCT. The revised flow diagram depicts information from four stages of a trial (enrollment, intervention allocation, follow-up, and analysis). The diagram explicitly shows the number of participants, for each intervention group, included in the primary data analysis. Inclusion of these numbers allows the reader to judge whether the authors have done an intention-to-treat analysis. In sum, the CONSORT statement is intended to improve the reporting of an RCT, enabling readers to understand a trial's conduct and to assess the validity of its results.
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Methodology of Clinical Trials Aimed at Assessing Interventions for Cutaneous Leishmaniasis
Piero L. Olliaro, Michel Vaillant, Byron Arana … (2013)
Introduction Why standardised methodologies for CL It is important to harmonize and improve clinical trial methodology for cutaneous leishmaniasis (CL); currently, treatment options are few and the quality of the supporting evidence is generally inadequate, making the strength of recommendations for the treatment of this disease inadequate. To improve on the case management and control of CL, better treatment modalities with reliable evidence of the efficacy, safety, tolerability and effectiveness is required. High-quality clinical trials are essential to determine which therapeutic interventions can confidently be recommended for treating which form of CL. Today, this is unfortunately not the case in numerous instances. The inadequacies of trials of different treatments of CL has been documented by two WHO-supported Cochrane systematic reviews [1], [2] which included 97 randomized controlled trials on treatments for Old World and American CL. They revealed critical issues related to the methodological quality of the design and reporting of these clinical trials, which make it difficult to compare results, meta-analyse the studies, and draw generalizable conclusions. Weaknesses ranged from the inadequacy of study design (including appropriate controls, endpoints, outcome measures, follow-up times), execution (randomization, allocation concealment, blinding), analyses and reporting (e.g. use of disparate endpoints) [3]. They also found a large number of trials that did not meet basic criteria, and could not be included in the analyses. This makes a highly compelling and cogent case for defining and harmonizing elements related to the design, conduct, analysis, clinical relevance, and reporting of trials, and ultimately study acquiescence by regulatory agencies. Improving the quality of studies and harmonizing protocols will make meta-analysis more informative and thus strengthen evidence for recommendations on treatment and case management. Furthermore, conducting inadequate trials may lead to inappropriate conclusion, is both unethical and an inefficient use of the limited resources available for research into this neglected disease. As heterogeneity is an inherent feature of CL (reflecting the variety of species and manifestations), there are obvious challenges in designing and interpreting trials to assess interventions for CL which will allow deriving generalizable results and recommendations. The objective of this paper is twofold: To provide clinical investigators with guidance for the design, conduct, analysis and report of clinical trials of treatments for CL. There is a particular need for standardized methodologies recognizing the complexity of the disease, and for defining measurable, reproducible and clinically-meaningful outcomes. To enhance the capacity for high-quality trials. It is clear that the limited resources available for CL have to be concentrated in clinical studies of excellence that fulfil the requirements to conduct good clinical studies and carried out according to international Good Clinical Practice (GCP) standards. It is also clear that disease-endemic countries must be assisted in acquiring the capacities to conduct these trials. This paper focusses on CL trial-specific issues; it only touches upon more general aspects of clinical trial conduct, which are extensively addressed in a number of relevant papers and documents. For instance the Global Health Trials website [4] offers several resources including a trial protocol tool [5]. Very diverse disease manifestations and responses to treatment The collective name of CL comprises several manifestations caused by different Leishmania species in the Old and the New World (OWCL and NWCL) and clinical trial methodology should be adapted to this spectrum of conditions. CL is caused by organisms of the L. mexicana complex and Viannia sub-genus (L. braziliensis and L. guyanensis complex) in the New World and L. major, L. tropica and L. aethiopica in the Old World. L. infantum in both Worlds and L. donovani in the Old World can also cause CL. The wide spectrum of clinical manifestations, natural histories and responses to treatment observed in CL patients is accounted for by the combination of parasite's intrinsic differences and patient's genetic diversity. The time required for natural cure (“self-healing”) is poorly defined and varies widely; it is generally accepted that lesions caused by L. mexicana in the New World and L. major in the Old World heal spontaneously in a time varying from a few weeks to several months in the majority of patients – except new foci (where the disease tends to be aggressive and self-healing is uncommon), and as opposed to other species (where spontaneous healing barely occurs or requires years). Bacterial super-infections are also frequent and can interfere with healing. The natural history of the disease must be accounted for when designing a clinical trial. Good knowledge of the disease characteristics at the trial site is essential; it is not possible to extract generalizable data from the published literature. For instance, when considering the placebo arms of randomised controlled trials (RCTs) from the Cochrane systematic review of OWCL1, 3-month cure rates for L. major were 21% in Saudi Arabia and 53% in Iran with oral placebo. With a topical placebo, they varied from 13% to 63% at 2 months in Iran and were 61% in Tunisia at 2.5 months. For L. tropica, cure rates were 0%–10% with oral placebo. In the New World, the information is scarce and more variable, ranging from 0% cure rate at one month in Panama [6] to 37% at 12 months in Colombia [7] for lesions most probably caused by L. panamensis. In Guatemala, using topical or oral placebos a 68% cure rate was reported at 3 months for lesions due to L. mexicana and only 2% for lesions due to L. braziliensis [8], while other studies have reported cure rates of 27% and 39% in the general population at 3 and 12 months respectively [9], [10]. In Ecuador, in a small group of 15 patients, a cure rate of 75% at 1.5 months (no speciation but likely L. panamensis) was reported without any treatment [11]. The examples above illustrate the need to acquire and factor in local data on the natural history of disease in order to assess more accurately treatment performance. A wide variety of treatment modalities has been reported for CL, but none has been shown to be universally effective. Treatment response varies according to a range of factors, including the Leishmania species, the patient immune status and age, the number and localization of the lesions, the severity of the disease, the treatment given and the route of administration, etc. Treatment would benefit both the individual patient but also reduce the burden of human reservoirs in the case of anthroponotic CL, and prevent super-infection and the resulting complications. The choice of treatment, either local or systemic, is usually based on the size, number and localization of lesions, lymphatic spread or dissemination, patient's immune status, cost, risk-benefit and the availability of the treatment itself in the country. Currently available treatment options (systemic and topical) can be found in the WHO 2010 technical report [12]. Defining trial participants The characteristics of the participants to be included must be adapted to the specific purpose of each clinical trial and must be representative of the typical patients seen in practice. The relevance of the spectrum composition of the study population to the range of patients seen in practice is of paramount importance especially in phase 3 an 4 trials. The factors that allow or disallow someone to participate in a clinical trial (“inclusion” and “exclusion” criteria, respectively), are used to identify appropriate participants and ensure both their safety and sound conclusions of the study. Establishing common grounds for entry criteria is also important in order to harmonize study populations across trials and facilitate comparability of trials and meta-analyses. It is also important to indicate the encatchment characteristics in terms of area and population, which would help in deciding as to the applicability of the findings of a trial, and ensure that the enrolled patients are representative of the larger patient population in that site (“spectrum composition”). Inclusion criteria Demography - Define: Gender - are both men and women to be included? CL tends to be gender-sensitive for exposure to infection in certain epidemiological settings (non-domestic and peri-domestic transmission foci), access to treatment and consequences of sequelae. In studies of CL both genders should be eligible for the study. Justify and provide rationale for any reason why either would not be eligible. For some (systemic) treatments, being pregnant or lactating or in child-bearing age may be exclusion criteria. If so required, a proper urine or serum pregnancy test must be documented as negative (generally within 48 hours prior to receipt of the first drug treatment). Repeating pregnancy tests at intervals in the study may be appropriate and should be considered for each study depending e.g. on the drug's residence time in the organism. Females within reproductive age are usually excluded from pre-licensure studies of most investigational new drugs or treatment interventions for safety considerations both for the fetus and the mother. Risks should be carefully weighed against benefits if it is decided to include women in child-bearing age and all necessary measures to prevent exposure during gestation should be set in place – though the risks may not be the same with systemic and topical treatments. Systematically excluding this group may however put them at a disadvantage. Age - all ages or adults only? Provide inclusive age range. In an ideal clinical study any individual with parasitologically confirmed CL would be included. Justify any age groups that would not be eligible for study. The age range will depend on a series of considerations, including the phase of study, the target population in a given area, type of treatment (e.g. invasiveness) and ethical considerations. For example, in early phases of the development of a new drug, most institutional review boards (IRBs) would want to see the drug studied in adults first. The age of the study population must be relevant to the actual population with the disease in a given setting (which, e.g., may be skewed towards young age groups). In addition, data exists showing that age is a determinant of response to treatment [13] possibly based on pre-existing immunity or different drug pharmacokinetics [14], [15] Form of the disease - Define: Which type of cutaneous form? Only localised cutaneous forms are within the scope of this protocol (see exclusion criteria). Morphology of the lesion - refers to the description of lesion appearance using classic dermatologic descriptive terms such as (see also Figure 1; specify which one and whether more than one are accepted): ulcer/ulceration (equivalent terms): meaning that at least part of the lesion is not covered with epidermis - a lesion covered with a crust is considered equivalent to an ulceration (if the crust is removed, the ulceration appears); papule: lesion raised above the skin surface, entirely covered with epidermis, palpable, main diameter smaller than 1 cm; nodule: the enlargement of a papule in three dimensions, solid, easily palpable and greater than 1 cm diameter) plaque: a palpable flat lesion (whether raised above the skin surface or not), greater than 1 cm diameter. Number of lesions - the number of discrete lesions allowed (single or multiple). The reasons for deciding whether all patients with confirmed CL are to be enrolled regardless of the number of lesions present, or only those with a single lesion should be documented and will mainly depend on the type of treatment administered; local treatments (e.g. physical heat treatments or topical creams) may prove either inadvisable (e.g. pain) or impractical to apply to multiple lesions. The number (and location – see below) of lesions vary with the geographic location and depends mostly on the efficiency of the vector; overall, 30–60% of patients will have one lesion, and >80–95% will have 5 YO >2 YO2 Adults >5 YO All Type of lesion3 Ulcers All All Ulcers All All Number of lesions 1–2 1–54 1–54 1–2 All All Size of lesions ≤30 mm5 ≤30 mm5 ≤30 mm5 ≤30 mm All All Localization Trunk, arms, legs Trunk, arms, legs, face6 Trunk, arms, legs, face6 Trunk, arms, legs All All Duration of lesion7 ≤3 months ≤6 months ≤6 months ≤6 months ≤6 months ≤6 months Parasitological confirmation Yes Yes Yes Yes Yes Yes Baseline lab tests, ECG, etc8. Yes/No No No Yes Yes No 1 Depending on available pre-clinical and reproductive toxicity data. 2 Age limit due to practical difficulties in measuring skin lesions in very small children. 3 Depending upon the Leishmania species and the type of treatment. 4 Due to practical difficulties in treating multiple lesions topically. 5 Due to practical difficulties in treating large lesions topically. 6 Topical treatment of lesions close to mucosae, eyes and ears is generally difficult and/or may pose safety hazard. Decision to include them in advanced phases of clinical evaluation depends on the risks associated with the specific delivery system or formulation used. 7 The decision to set a limit for the lesion age should take into consideration a) the Leishmania species –probability that lesions will self-heal within the study time; and b) the difficulty in accurately establishing the age of the lesion from interviewing the patient due to recall bias. 8 Depending on the risk of systemic toxicity based upon pre-clinical toxicity and clinical data available and the route of administration. Endpoint - outcome measures and therapeutic assessment The protocol must identify clearly primary and secondary endpoints for efficacy and safety. The primary efficacy endpoint must be both accurate and robust; the protocol should clarify how and when cure is defined. It is advisable to focus the research on few endpoints that are feasible and attainable within the study, and avoid multiple, diffuse endpoints. Harmonizing efficacy endpoints is essential to allow comparing study results and conducting meta-analyses. Any procedures applied which may interefere with healing should be standardised upfront and reported in sufficient details. Such would be the case, for standard of care, including dressing, debridement and cleaning of ulcers before and during treatment. Efficacy parameters Cure should be defined on clinical parameters It is generally agreed that cure should be defined based on clinical parameters. Early studies showed that parasitological examination at the end of therapy correlates poorly with the final treatment outcome [26] and relatively few studies have since based their definition of cure on a parasitological outcome. However, it must be pointed out that, for licensure studies, this point may have to be discussed beforehand with regulatory authorities (which will have no particular knowledge of the disease, and apply traditional clinical microbiology criteria). Ulcer surface area should be the primary efficacy endpoint, whenever possible Ideally, a clinically accurate definition would include a combination of five parameters (Figure 2): (i) area of ulceration, when present (x by y), (ii) area of induration (x′ by y′), (iii) thickness of induration (z), (iv) colour of infiltrated border, and (v) degree of scaring as a proxy for patient's quality of life. 10.1371/journal.pntd.0002130.g002 Figure 2 Measuring lesions. However, colour and thickness are prone to inter-observer variations and difficult to measure, and quality of life is highly subjective. There is, however, increasing general attention on patient-reported outcomes (PRO) being used as study endpoints. Research into properly constructed PROs should be encouraged. Specifically for CL, this would apply in particular to cosmetic endpoints, like scar assessment methods. Ulceration area (after debridement and cleaning) is the easiest parameter to measure, and is also clinically meaningful. There is recent evidence that ulceration and induration have parallel evolutions, so both accurately reflect lesion evolution (Buffet, Ben Salah, Grögl et al. Unpublished data). When should induration be used instead of ulcer? For species causing predominantly nodular lesions (L. infantum, L. mexicana, L. aethiopica), induration area should be used to measure treatment effects. Measuring induration is more difficult than measuring ulcers, and requires training of the study team on e.g. the ball-pen technique, to ensure inter-observer reproducibility. Only areas of “red” or “inflamed” induration should be considered, while hypertrophic scars (where induration no longer reflects an active lesion but rather an aberrant scarring evolution) should be discounted. Induration should also be used to capture relapses manifesting as purely nodular lesions (i.e., no ulceration). This is a rare situation where parasitological examination should be performed in order to ascribe the new lesion to the parasite. Satellite lesions occur in 5–8% of the CL caused by L. tropica. These classical lesions do not always contain abundant parasites and may not require parasitological examination, which is invasive. When should cure be assessed? The use of single time point at which cure rates are compared between arms is simple and practical, but not fully informative. Time to cure is also important for self-healing CL. Actuarial analysis of multiple sequential observations (e.g. product-limit estimate of time-to-cure using Kaplan-Meier analysis) is also possible though more cumbersome and care must be exercised not to over-estimate clinically non-relevant differences – see section on survival analysis below. Clinical trials conducted between the late 80's and early 2000's [8], [10], [27]–[29] showed that tissue repair may take several weeks after the causal factor has been removed (i.e., parasites have been killed). Empirically, 6–9 weeks after treatment start is a reasonable compromise – it leaves enough time for most lesions to heal, yet it is not too long for a patient receiving placebo or an ineffective treatment to receive rescue treatment. In order to both harmonise and simplify procedures, treatment outcome should be assessed on three occasions (counting from the first day of treatment): Day 42–63 (6–9 weeks) for “initial response”, in order to identify early failures. The range is to allow for different healing rates for L. major, L. mexicana (Day 42) and other species (L. tropica, most of the NWCL, Day 63). Day 90±1 week (3 months) for “initial cure”, and Day 180–360±2 weeks (6–12 months) for “definitive cure”, in order to allow for long-term relapses. The overall duration of follow-up will be based on local data on the natural history of disease, as well as practical considerations (e.g. dropout rates with longer follow-up) Visists in-between the above are also encouraged, when feasible. For a unified, standardised efficacy reporting, a simple, dichotomous outcome definition as either “cure” or “failure” should be adopted, whereby “cure” can only be declared at the end of follow-up (Day 180–360), whereas “failure” can occur at any time (and will require rescue treatment). Figure 3 describes the decision-tree. 10.1371/journal.pntd.0002130.g003 Figure 3 Decision tree for the assessment of treatment outcome. Ø = complete re-epithelialisation; 50% = greater than 50% of the initial size. “Cure” is defined as: An ulcer that on Day 42–63 is completely re-epithelialised (Ø) and remains so on both Days 90 and 180–360 (no relapse) An ulcer that on Day 45 is 50% of the initial size An ulcer whose size is >Ø at Day 90 or Day 180–360, irrespective of whether it had been re-epithelialised (Ø) before (relapse) Depending on the natural history of the diseases or its local epidemiological characteristics, additional, secondary parameters may be used to qualify cure, such as the absence of induration, redness or papules around the lesion, or, in case of papules and nodules, parasitological positivity – though after due consideration of its significance. Safety parameters The assessment and reporting of the safety, toxicity and tolerability of treatments, while an essential component of the evaluation, is often overlooked in CL clinical trials. Topical treatments may produce local events at the site of the lesion (like irritation); systemic treatments may cause generalised signs or symptoms, including changes in laboratory values. Events should be reported and graded using standard nomenclature and criteria of severity. Whenever possible, events must be combined under a syndrome or diagnosis. It is important to comply with regulations for filing serious events; specific requirements exist for timely reporting accoriding to national regulations (health authorities, regulatory authorities, ethics committees). However, investigators must be alerted to the fact that definitions and rules for reporting may evolve with time and are not fully harmonised between countries. Definitions – it is important that clinical trialists understand and use the appropriate definitions - see e.g. relevant documents by the International Conference for Harmonization (ICH; specifically the E6 Guidance on GCP and the E2A guidance on Clinical Safety management [30]), the European Medicines Agency (EMA) [31] and the US Food and Drugs Administration (FDA) [32]. All events, whether considered drug-related or not, should be recorded (adverse event, AE) [33]. An AE is any untoward medical occurrence in a patient or clinical investigation subject administered a pharmaceutical product and which does not necessarily have a causal relationship with this treatment. An AE can therefore be any unfavourable and unintended sign (including an abnormal laboratory finding), symptom, or disease temporally associated with the use of a medicinal (investigational) product, whether or not related to the medicinal (investigational) product. When a causal relationship with the treatment is established or suspected (“reasonable possibility”) by the investigator, an AE is defined as adverse drug reaction (ADR). In the case of a new medicinal product (aka “investigational new drug”, IND) or its new usages, the ICH guidelines indicate that any noxious and unintended responses should be reported as suspected adverse reaction (SAR) as the drug-event relationship cannot be ruled out. In the case of marketed products an ADR is defined as an event which occurs at doses normally used in man for prophylaxis, diagnosis, or therapy of diseases or for modification of physiological function. It is generally recommended that “ADR” be preferred over “side effect”. When the AE is “unexpected”, this defines a UAE (Unexpected Adverse Event) – not encountered before (i.e. not in the drug Investigator Brochure for a new product, or not in the summary of product characteristics for a marketed drug) or not at the observed severity, whether it may be anticipated from the pharmacological profile of the drug under investigation or drugs belonging to the same class. When the AE meets the criteria of being “serious” (which is different from “severe”), this is considered a Serious Adverse Event (SAE). An SAE is any untoward medical occurrence that results in death, is life-threatening, requires inpatient hospitalization or prolongation of existing hospitalization, results in persistent or significant disability/incapacity, or - is a congenital anomaly/birth defect. Requirements for reporting. According to the ICH guidelines, the clinical investigator must report an SAE immediately to the sponsor, which in turn must report the event to the relevant authority if the SAE is considered drug-related and unexpected (Serious Unespected Suspected Adverse Reaction, SUSAR). In case the investigator is also the sponsor, s/he has to fulfil all sponsor's responsibilities. Specific local requirements must be taken into account, too. When analysing the events, the comparison with baseline (pre-treatment, aka “medical history”) allows defining treatment-emergent AE (TEAE) - defined as any event (sign, symptom, laboratory abnormality) which was either not present prior to the initiation of the treatment or worsened (in either intensity or frequency) with the treatment. Using TEAE helps separating those events that preceed treatment (related to the disease or to the subject's pre-existing conditions) from those that occur or worsen with the treatment. In order to be able to analyse and report on TEAEs, the occurrence and intensity of events must be recorded at baseline (before the treatment is administered), as well as any time post-treatment, and the occurrence and intensity compared. Terminology- it would be useful to harmonise the terminology to identify events; while proprietary medical dictionaries exists, the WHO International Classification of Diseases (ICD) is free and can be used for the purpose [34]. Grading - for grading intensity of events (mild, moderate, severe, very severe), use standardised criteria, e.g. the Common Terminology Criteria for Adverse Events (CTCAE) (version 4.03 [35]) or the Division of Microbiology and Infectious Diseases (DMID), National Institute of Allergy and Infectious Diseases (NIAID), National Institute of Health (NIH) adult and paediatric toxicity tables [36]. It would be useful to consider developing CL-adaped CTCAE criteria. Drug-event relationship – it is often difficult to establish and subjective, and depends on previous experience with the use of a treatment. There are therefore differences in the appreciation of events between established and new products, which may introduce biases in unblinded clinical trials. Definitive evidence can only come from de-challenging (the effect disappears) and re-challenging (the effect represents) but this procedure is often difficult to apply. Study design This section treats of study design with a specific focus on issues of special relevance to comparing treatments for CL. In this context, we delve more into types of design (such as non-inferiority trials, adaptive designs) that the typical CL investigator might be less familiar with. According to the recent WHO treatment recommendations for leishmaniasis, including CL, there are cases (e.g. uncomplicated L. major) where an unfavourable risk-benefit ratio (resulting from the combination of a self-curing lesion and the lack of an effective and safe treatment) means that no treatment may currently be recommended (and thus no standard treatment exists to which to compare) [12]. In other cases, cure rates up to or above 90% have been reported following different treatments, though results depend also on the duration of follow-up [1], [3]. However, even when efficacy is high, the risk-benefit of some such treatments is not always well-established, or in favour of the intervention (e.g. systemic toxicity associated with the use of parenteral antimony). These elements must be accounted for when designing a clinical trial for any specific form of CL. These trials will belong to either of the following types: Phase 2 (safety and dose-finding studies to select the dose and duration of treatment which is safe and effective to be tested further in larger efficacy studies); Phase 3 (randomized controlled trials (RCTs) to establish the value and support the registration of a new intervention with superiority design (over reference treatment or placebo) or non-inferiority design (against a reference standard treatment); or Phase-4 trials (post-registration, when the new treatment is being implemented in the field in conditions that are closer to real life). All studies, whether with or without a direct external comparison, should have at least two arms and be randomized, with few exceptions. Randomized comparative designs Comparator (reference) intervention Current WHO recommendations [12] provide for multiple options, including no treatment, topical or systemic treatment, depending on the species and clinical judgment. Therefore the choice of the reference treatment will have to based largely on local experience and expert opinion – yet supported by reliable data. According to the International Conference for Harmonization (ICH) [37], the choice of a control group should consider its ability to minimize bias, ethical and practical issues associated with its use, usefulness and quality of inference, modifications of study design or combinations with other controls that can resolve ethical, practical, or inferential concerns, and its overall advantages and disadvantages. The guidelines include five types of control groups: i) placebo, ii) no treatment, iii) different dose or regimen of the study treatment, iv) a different active treatment, v) external historical controls (the latter being of very limited use as it carries important biases and raises serious concerns as to between-groups comparability). Few cases will warrant a placebo or no-treatment arm unless this is as an ‘add-on’ to generally accepted (partially) effective treatment [38]. The choice of giving patients no treatment or a placebo must be on solid scientific and ethical foundations. A no-treatment arm may be justified in case of uncomplicated, self-healing lesions and will provide much needed information on the natural history of disease upon which future studies can be built – although this may be site-specific and non-generalizable. Such an option will however depend on ethical considerations and local regulations. It is important to be clear as to what is meant by “placebo”; as a placebo should match the active drug, it may be oral or topical – it is difficult to conceive an injectable placebo. Between the two, the only genuine placebo is oral. Basic interventions like cleaning and protecting the lesion against super-infections, as well as topical placebos are known to modify the natural history of the disease, and will likely accelerate the self-healing rate. For clarity, the term “vehicle control” should be preferred over “topical placebo” when it is made of a cream or ointment with only excipients and no active ingredient. This effect on wound healing should be considered in placebo-controlled trials, though the increased cure rate obtained with the intervention over and above “topical placebo” will be difficult to quantify. Superiority design Whatever the comparator, superiority randomized controlled trials (RCTs) are intended to provide evidence that the test intervention is superior to the control intervention. Calculations and examples follow. The basic statistical elements to be considered in designing a trial are summarized in Box 1. Box 1. Statistics – Definitions α (probability of a type I error) is the probability of erroneously rejecting the null hypothesis (i.e. recommending a medicine with no advantages) given that the null hypothesis is true; β (probability of a type II error) is the probability of erroneously failing to reject the null hypothesis (i.e. keeping a good medicine away from patients) given that the alternative hypothesis is true 1- β (power) quantifies the ability of the study to find true differences of various values of δ (see below). It expresses the chance of correctly identifying the alternative hypothesis, and to correctly identifying a better medicine. Δ is the minimum difference between groups that is judged to be clinically important - i.e. the minimal effect which has clinical relevance in case management. The choice of the values of type one error rate, α, and power, 1- β (i.e. how stringent the study will be), as well as the expected cure rates with the control and the improvement to be detected for the test intervention will determine the sample size of the study. Noteworthy, reliable efficacy data for the comparator arm are needed; wrongly estimating the efficacy of the comparator treatment may result in the study being underpowered, hence failing to produce the intended results. When the number of arms is >2 (i.e. >1 test intervention or dose), this will have to be accounted for in sample size calculation and result in a larger sample size per group, other things being equal, in order to allow for multiple comparisons. The study may be designed to compare proportions (cure rates) between the control and test intervention, but also means (e.g. of size of lesions). A non-significant result (i.e. no significant difference detected) does not imply that the two treatments are equal [39]. Examples of assumptions and their implications in terms of sample size calculations are provided in Figure 4 and Table 2, assuming: a two-tailed test, α = 0.05; power (1-ß) = 0.80, 0.85 or 0.90; success rate of the comparator drug = 60–90%; and δ = 10–30%. The larger the δ, and the more effective the reference intervention, the smaller the sample size. In the typical example of a superiority design with the reference treatment being 80% effective, expecting a 10% difference with the test treatment (90% effective) with power = 0.80, 199 patients per arm would need to be recruited. For comparison, a 10% difference with a reference treatment that is 70% effective will require 294 patients. 10.1371/journal.pntd.0002130.g004 Figure 4 Sample size calculations for comparative superiority trials. 10.1371/journal.pntd.0002130.t002 Table 2 Sample size calculations for superiority trials. Control treatment Success Rate Test treatment Success Rate Power N Per Group 0.6 0.7 0.80 356 0.6 0.7 0.85 407 0.6 0.7 0.90 477 0.6 0.7 0.95 589 0.6 0.8 0.80 82 0.6 0.8 0.85 93 0.6 0.8 0.90 109 0.6 0.8 0.95 134 0.6 0.9 0.80 32 0.6 0.9 0.85 36 0.6 0.9 0.90 42 0.6 0.9 0.95 52 0.65 0.7 0.80 1377 0.65 0.7 0.85 1575 0.65 0.7 0.90 1842 0.65 0.7 0.95 2278 0.65 0.8 0.80 138 0.65 0.8 0.85 158 0.65 0.8 0.90 185 0.65 0.8 0.95 228 0.65 0.9 0.80 43 0.65 0.9 0.85 49 0.65 0.9 0.90 57 0.65 0.9 0.95 70 0.7 0.8 0.80 294 0.7 0.8 0.85 336 0.7 0.8 0.90 392 0.7 0.8 0.95 485 0.75 0.8 0.80 1094 0.75 0.8 0.85 1251 0.75 0.8 0.90 1464 0.75 0.8 0.95 1810 0.75 0.9 0.80 100 0.75 0.9 0.85 114 0.75 0.9 0.90 133 0.75 0.9 0.95 164 0.8 0.9 0.80 199 0.8 0.9 0.85 228 0.8 0.9 0.90 266 Efficacy in the reference arm from 60–80%, delta 10–30%, alpha error 0.05, power 80–95%. In addition, in calculating the sample size, allowance should be made for losses to follow-up - a parameter which is very much site-specific. The intent-to-treat (ITT) is generally considered the choice population for analysis; it comprises all patients randomized who gave informed consent and received any amount of the assigned intervention at least once. The practical problem in applying ITT is that it requires measurement on all patients whether or not they are still adhering to the protocol. Thus as soon as one has ‘loss to follow-up’ it is not possible to apply a pure ITT analysis. This population reflects treatment effects in conditions that are closer to those encountered in routine use, as opposed to the per-protocol (PP) population, which is restricted to the patients without major protocol deviations who are evaluable at the planned visit for efficacy assessment and thus measures the pure treatment effect (“evaluable patients' analysis”). The mITT population definition is used to overcome the bias of the ITT population. It is a subset of the ITT population allowing for the exclusion of patients due to non compliance or missing outcome. Conclusions will be drawn from the results on the primary criteria calculated on the ITT or the modified-ITT (mITT) population. Non-inferiority design Non-inferiority trials are intended to show that the new intervention is no worse than the standard drug by some margin Δ (the non-inferiority margin), defined as the largest clinically acceptable difference [40]; it should be smaller than differences observed in superiority trials of active comparator [41]. The non-inferiority design has become increasingly popular in malaria and tuberculosis (where very effective treatments exist), but is rarely used in leishmaniasis; so far, it has been used for visceral leishmaniasis (VL) randomized controlled trials in India [42], [43] and East Africa (DNDi clinical trials.gov NCT01067443). The choice of the non-inferiority margin is very important as it governs the validity of the trial, and has also ethical implications [44]. The objective is to avoid harmful treatment to be declared non-inferior, and to retain a treatment that brings a true benefit for the patient [41]. The decision should be based on previous studies with the reference treatment and the minimally important effect that one wants to observe with the new treatment which would provide additional benefit for the patients. In order to identify the correct Δ, it has also been proposed to compare (i) the two-sided 95% confidence interval of the difference between the test and the reference treatment to (ii) a two-sided 95% CI of the difference between the reference treatment and the placebo based on historical data and meta analyses (if such data are available) [45]. Virtual comparison methods are also available, whereby the new treatment is compared to a putative placebo by synthesizing the estimated effectiveness of the former versus an active control and the estimated effect of the latter versus the placebo [46]. It is important to note that defining the Δ is not a mere statistical exercise; it requires consideration of what is a clinically acceptable failure rate, in the context of other factors, such as practicalities (duration of treatment, route of administration) and costs. Calculations and examples follow. The basic elements to be considered in designing a non-inferiority trial are similar to those of a superiority design. The difference is in the choice of the margin and the test used to compare the treatment estimates. When success or failure rates are used to measure treatment effects, it is common to compare the 95%CI lower limit to the non-inferiority margin. However, in the case of proportions, it should be also of interest to compare risk ratios (RR) or odds ratios (OR) with a non-inferiority margin specified on the RR or OR scale. In the examples that follow we work with proportions and 95%CI. The sample size is calculated based on the expected proportion of events in the reference arm (80%, 85%, 90% or 95%), the expected true difference in proportions between the reference and the tested treatment arms (0%), α risk = 0.01, unilateral hypothesis, and power (1-ß) = 90% the equivalence margin defined as acceptable for concluding that a tested treatment is not inferior to the reference arm (from 5% to 10%; meaning that one is prepared to accept that the test treatment is 5% or 10% less effective than the reference treatment). The larger the Δ, and the more effective the reference intervention, the smaller the sample size. Using a reference treatment that is 80% effective, the sample size varies from 1667 (5% Δ) to 417 (10% Δ); similarly, for the same Δ = 10%, the sample will be 124 when the reference treatment is 95% effective. The total sample size would allow an assumption on the expected proportion of drop-outs (5% for instance) and multiply by 2 (groups). In case of more than 2 groups being studied, the calculation will have to allow for an adjustment for multiplicity such as the so-called Bonferoni correction. More results are presented in Figure 5 and Table 3. 10.1371/journal.pntd.0002130.g005 Figure 5 Sample size calculations for comparative non-inferiority trials. 10.1371/journal.pntd.0002130.t003 Table 3 Sample size calculations for non-inferiority trials. Non-inferiority margin Reference treatment Success Rate N Per Group −0.05 0.80 1667 −0.05 0.85 1328 −0.05 0.90 938 −0.05 0.95 495 −0.06 0.80 1158 −0.06 0.85 923 −0.06 0.90 651 −0.06 0.95 344 −0.07 0.80 851 −0.07 0.85 678 −0.07 0.90 479 −0.07 0.95 253 −0.08 0.80 651 −0.08 0.85 519 −0.08 0.90 367 −0.08 0.95 194 −0.09 0.80 515 −0.09 0.85 410 −0.09 0.90 290 −0.09 0.95 153 −0.1 0.80 417 −0.1 0.85 332 −0.1 0.90 235 −0.1 0.95 124 Efficacy in the reference arm from 80%–95%, delta 5–10%, alpha error 0.01, power 90%. The Non-inferiority margin represents the smallest acceptable difference with respect to the success rate with the reference treatment. These calculations show the importance of the non-inferiority margin and the proportions for the reference treatment. When the α risk and power are fixed, the sample size can grow exponentially whenever a little change is done in the assumptions. Between the ITT and the PP populations, ITT may bias the results toward equivalence, which could make a truly inferior treatment appear non-inferior [41], [47]–[49]. ITT analysis carries the risk of falsely claiming non-inferiority [50] although this may not always be the case [51] (reviewed and discussed in Piaggio et al [52]). According to Abraha et al [47], in non-inferiority trials “excluding participants who did not adhere fully to the protocol can be justified. Exclusions may, however, affect the balance between the randomized groups and lead to bias if rates and reasons for exclusion differ between groups [53], [54]”. The current thinking of regulatory agencies is that the study objective should be achieved in both the ITT and PP populations, especially in a non-inferiority trial [40]. However, Maltilde-Sanchez et al [55] argue that this “does not necessarily guarantee the validity of a non-inferiority conclusion and a sufficiently powered PP analysis is not necessarily powered for ITT analysis”. These authors propose to perform a new maximum likelihood-based ITT analysis arguing that it could address “the potential types and rates of protocol deviation and missingness that might occur in a non-inferiority trial” and that “prior knowledge regarding the treatment trajectory of the test treatment versus the active control at the design stage” should be collected “so that a proper analysis plan and appropriate power estimation can be carried out”. Illustrating the divergent conclusions toward non-inferiority between the ITT and PP populations is outside the scope of this work. Neverthless the examples provided in Table 4 (which use rates derived from published NWCL studies at 6–12 months of follow-up) illustrate how much exclusions can influence the sample size required to prove non-inferiority: the more patients are excluded and the less effective the reference treatment is, the larger the sample size required for a given non-inferiority margin – obviously the sample size decreases when the non inferiority margin increases. This means that different conclusions as to non-inferiority may be reached on the ITT vs. the PP populations. Therefore, special attention must be paid to minimizing losses to follow-up and numbers of patients deemed non-assessable, both of whom would be deducted from the PP population. 10.1371/journal.pntd.0002130.t004 Table 4 Samples size calculation (N per group) for non-inferiority trials. reference treatment success rate delta exclusions 60% 65% 70% 75% 80% 85% 90% 6% 0% 1736 1646 1519 1356 1158 923 651 5% 1823 1728 1595 1424 1216 969 684 10% 1910 1811 1671 1492 1274 1015 716 15% 1996 1893 1747 1559 1332 1061 749 20% 2083 1975 1823 1627 1390 1108 781 25% 2170 2058 1899 1695 1448 1154 814 8% 0% 977 926 855 763 651 519 367 5% 1026 972 898 801 684 545 385 10% 1075 1019 941 839 716 571 404 15% 1124 1065 983 877 749 597 422 20% 1172 1111 1026 916 781 623 440 25% 1221 1158 1069 954 814 649 459 10% 0% 625 593 547 489 417 332 235 5% 656 623 574 513 438 349 247 10% 688 652 602 538 459 365 259 15% 719 682 629 562 480 382 270 20% 750 712 656 587 500 398 282 25% 781 741 684 611 521 415 294 Success rate ranging 60–90%; exclusions ranging 0–25%; non-inferiority margin (delta) 6%, 8% and 10%. Other randomized designs Precision estimate A precision estimate can be used when one can estimate success/failure rates or means as well as mean difference from previous studies done in a different environment or time period. The objective is therefore to evaluate this estimate and its variability in a new population. Examples of sample size with precision estimate [56] if the required success rate is The precision estimate is used in the case of non-comparative design, therefore it cannot judge the efficacy of a treatment comparatively to placebo or an active treatment. It could be used however for dose-finding. Adaptive designs These designs are meant to allow choices amongst various drugs and regimens (dose, duration) systematically, as quickly and effectively and with as few patients as possible. The term includes group sequential designs, sequential methods and methods to stop earlier trials with superiority or non-inferiority designs. Adaptive trials designs are increasingly used to improve efficiencies in the R&D process. This approach allows redesigning the trial based on the information acquired through interim analyses, which may result in changing the sample size, the number of arms, or other elements. Sequential and group sequential trials are a special case of adaptive trials where several interim analyses are done in order to complete earlier the trial based on the accumulated information. We will concentrate here on sequential methods, and more specifically on the Whitehead triangular test, a graphical methods defining with boundaries which allows for early rejection or non-rejection of H0. Examples using the Whitehead triangular test [57] follow. In this example, the hypothesis to be tested will be a difference of 8% between the failure rate (in %) of each group and the boundaries calculated for 10 discrete stages of evaluation. The type I and type II risk are commonly set at α = 0.05, power (1-ß) = 0.80 i.e. the risk to reject an effective treatment is 5% and the chance for the study to find an effective treatment is 80%. The null proportion is set at 0.1 and the alternate proportion is set at 0.18, 0.20 and 0.25. These assumptions mean that if the failure rate <10%, efficacy is considered adequate, and if the failure rate ≥25% efficacy is insufficient. In terms of probabilities, it can be written that the boundaries of the test are calculated for H0(p≥p0) and Ha(p
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Fluconazole for the treatment of cutaneous leishmaniasis caused by Leishmania major.
B. De La Cruz, Abdulrahman Alrajhi, Yehia M Khairat … (2002)
Whereas certain oral antifungal azoles are well documented to have activity against leishmania, data on the efficacy of fluconazole for leishmaniasis are limited. We conducted a controlled trial in Saudi Arabia of fluconazole for the treatment of cutaneous leishmaniasis caused by Leishmania major. This randomized, double-blind, placebo-controlled trial assessed the efficacy of oral fluconazole, in a dose of 200 mg daily for six weeks, in the treatment of parasitologically confirmed cutaneous leishmaniasis. The primary outcome measure was the time to the complete healing of all lesions. A total of 106 patients were assigned to receive fluconazole, and 103 patients were assigned to receive placebo. Follow-up data were available for 80 and 65 patients, respectively. At the three-month follow-up, healing of lesions was complete for 63 of the 80 patients in the fluconazole group (79 percent) and 22 of the 65 patients in the placebo group (34 percent; relative risk of complete healing, 2.33 [95 percent confidence interval, 1.63 to 3.33]). According to an intention-to-treat analysis, the rates of healing were 59 percent and 22 percent, respectively (relative risk, 2.76 [95 percent confidence interval, 1.84 to 4.12]). Sodium stibogluconate was offered to 11 patients in the fluconazole group who returned for follow-up (14 percent) and 33 of those in the placebo group (51 percent) in whom oral treatment was judged to have failed. According to a Kaplan-Meier analysis, the time to healing was shorter for the fluconazole group (median, 8.5 weeks, as compared with 11.2 weeks in the placebo group; P<0.001 by the log-rank test). Side effects were mild and similar in both groups. A six-week course of oral fluconazole is a safe and useful treatment for cutaneous leishmaniasis caused by L. major.
Author and article information
Contributors
Endi Lanza Galvão:
ORCID: http://orcid.org/0000-0002-5648-3932
Role: Data curationRole: Formal analysisRole: InvestigationRole: MethodologyRole:
Writing – original draft
Ana Rabello: Role: SupervisionRole: Writing – review & editing
Gláucia Fernandes Cota: Role: ConceptualizationRole: Data curationRole: Formal analysisRole: MethodologyRole:
SupervisionRole: Writing – review & editing
Henk D. F. H. Schallig: Role: Editor
Journal
Journal ID (nlm-ta): PLoS One
Journal ID (iso-abbrev): PLoS ONE
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PLoS ONE
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October
2017
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Volume: 12
Issue: 10
Electronic Location Identifier: e0186117
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* E-mail:
endi.lanza@
123456cpqrr.fiocruz.br
Author information
Endi Lanza Galvão
http://orcid.org/0000-0002-5648-3932
Article
Publisher ID: PONE-D-17-24802DOI: 10.1371/journal.pone.0186117
PMC ID: 5633178
PubMed ID: 29016694
SO-VID: a7e5b534-7547-4d65-8fb1-b880f45c434d
Copyright © © 2017 Galvão et al
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This is an open access article distributed under the terms of the Creative Commons Attribution License, which permits unrestricted use, distribution, and reproduction in any medium, provided the original author and source are credited.
History
Date
received
: 30
June
2017
Date
accepted
: 25
September
2017
Page count
Figures: 6,
Tables: 8,
Pages: 24
Funding
AR is currently receiving a grant [311641/2009-1] from CNPq (National Counsel of Technological
and Scientific Development). ELG is a Ph.D. student and is receiving a scholarship
from FAPEMIG (Foundation for Research Support of the State of Minas Gerais). The authors
received no specific funding for this work.
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