Session IV
S. R. Norrby
Design of Clinical Trials in Patients with Urinary Tract Infections Summary: This overview deals with the optimization of the design of clinical trials in patients with urinary tract infections (LrFIs). Despite the fact that LrFI is one of the most common types of infection and that the main end-point (elimination or persistence ~of bacteriuria) is objective and easy to register, the quality of studies performed and published has generally been less than optimal. Problems that should always be addressed in the study protocol are definitions of terms used, for example bacteriuria, level of the infection (cystitis or pyelonephritis), and uncomplicated and complicated infections; dimension of the patient's sample to allow adequate testing of a null hypothesis; procedures before, during and after treatment; methods for analysis of the results. Zusammenfassung: Studiendesi..gn bei Patienten mit Harnwegsinfektionen. In diesem Uberblick wird die Optimierung klinischer Studien bei Harnwegsinfektionen (HWI) dargestellt. Obwohl HWI zu den h/iufigsten Infektionskrankheiten gehfren und der Endpunkt (Eliminierung'oder Persistenz der Bakteriurie) objektiv und leicht festzustellen ist, zeigt sich, dab die Qualit/it der durchgefiihrten und publizierten Studien im allgemeinen nicht optimal ist. Es ist wichtig, dab in allen Studienprotokollen folgende Gesichtspunkte beriicksichtigt werden: Definition der verwendeten Begriffe, z. B. Bakteriurie, Ebene der Infektion (Zystitis oder Pyelonephritis) sowie unkomplizierte und komplizierte Infektion; der Umfang der Patientenstichprobe, um die Nullhypothese ausreichend zu testen; MaBnahmen vor, w/ihrend und nach der Therapie; Methoden zur Analyse der Ergebnisse.
Introduction Antimicrobial agents differ from other types of drug in that they ideally have no effect on the host; any such effect is a potential adverse reaction. Instead, they interact with the pathogens that cause infection. Thus, the pharmacodynamics of antimicrobial agents are the interactions between the drug and the microbe, not between the drug and the host. From these interactions follows a potential risk of ecological side-effects caused by unwanted disturbances of the normal microbial flora of the patient treated. Clinical trials of antimicrobial agents have tended to be of generally low quality [1-3]. There are several reasons for this; (I) the end-points used are often dichotomous, i.e. outcome is expressed in terms such as cured versus improved or bacterial eradication versus bacterial
persistence, necessitating very large patient samples, (II) factors other than the infection itself, e.g. underlying diseases or immunodeficiencies, influence the outcome of treatment and make the evaluation of the effects of the drug per se difficult, (III) end-points are often subjective rather than objective, and (IV) medical interventions other than drug treatment, such as surgical drainage of purulent infections, are often critical for the cure of an infection. Despite the fact that, for reasons discussed below, urinary tract infections (UTIs) are among the easier types of infection to study, the quality of the majority of UTI trials has also been low [2]. In the following discussion about the design of clinical trials in patients with UTI, it is important to realize that UTI constitutes a group of infections which vary considerably with regard to treatment, duration and prognosis. Extrapolation of results obtained in one type of UTI to another type is therefore not normally possible. This overview will not deal with registration and analysis of safety, nor with ethical aspects since in that context UTI does not differ from other infections.
Guidelines for Clinical Trial Design General guidelines for the design of clinical trials of antimicrobial agents have been published by the British Society for Antimicrobial Chemotherapy (BSAC) [4,5]. Such guidelines, as well as specific ones, have been published by the Infectious Diseases Society of America (IDSA) under contract with the U.S. Food and Drug Administration (FDA)[6]. The World Health Organization is also in the process of publishing guidelines for trials of antimicrobials [7]. The IDSA/FDA document includes specific guidelines for several types of infections, including UTI. Efforts are in progress to use the IDSA/FDA guidelines as a format for a European counterpart. This would allow a greater degree of cooperation between US and European investigators and eliminate some of the repetitive studies now being performed on both sides of the Atlantic. Finally, there are several documents regulating Good Clinical Practice (GCP) for clinical trials, that is, the general requirements for the conduct of clinical trials with regard to relations between the pharmaceutical industry and investigators monitoring the trials etc. [7].
Definitions In all clinical trials, the terminology used must be clear and defined. Internationally acceptable definitions are preferable. However, such definitions are often lacking S. R. Norrby, M. D., Ph.D., Dept. of InfectiousDiseases,Lund University Hospital, S-22185 Lund, Sweden.
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S. R. Norrby: Clinical Trials in UTI and must then be agreed before the trial is started, and included in the study protocol. For IYFI, the following definitions are proposed: Significant bacteriuria can be defined in several ways. Kass [8] in his classical study defined it as -> 105 colony-forming units (cfu) per ml of a midstream urine sample or any bacterial count in a sample obtained by bladder puncture. Stature et al. [9] found that, in midstream urine samples, UTI defined as bacterial counts of -> 10z cfu/ml gave the highest specificity and sensitivity. However, if these lower counts are accepted, it is important to realize that sampling procedures must be optimized and the samples be kept refrigerated during the entire interval between micturation and inoculation at the laboratory. It should be noted that studies on the break-points for significant bacteriuria have concentrated on gram-negative organisms. In infections caused by Staphylococcus saprophyticus and possibly also other staphylococci, a lower break-point should be used, since these organisms clump together and each colony represents many organisms. In this respect it is also important to decide beforehand how samples yielding more than one bacterial species should be interpreted. In patients with bladder catheters two or even three strains may be present in the urine. Patients who are not catheterized and who have symptomatic infections, on the other hand, normally have only a single strain in their urine and samples yielding two or more strains should be regarded as contaminated. The classification of UTIs by the level of the urinary tract affected into cystitis (lower) and pyelonephritis (upper) seems simple but is often very difficult in clinical practice. The typical symptoms of pyelonephritis, fever and loin pain, may be masked by the intake of analgesics, which often also act as antipyretics. Laboratory tests, for example the measurement of C-reactive protein (CRP), presence or absence of casts by urine microscopy, and reduced urine osmolarity following challenge with antidiuretic hormone, may assist in the diagnosis. The value of testing for the presence in urine of antibody-coated bacteria (ACB) is more doubtful. This test has either a low specificity or a low sensitivity, depending on which frequency of ACB-positivity is chosen as indicative of pyelonephritis. In protocols for trials that include patients with pyelonephritis, the diagnostic criteria must be clearly defined. In both pyelonephritis and cystitis, the prognosis varies according to the type of infection. The infections must be classified as being symptomatic or a.~mptomatic. Asymptomatic infections include asymptomatic bacteriuria (ABU) for which the diagnostic criteria are stricter than for symptomatic infections (at least two midstream urine samples are required) [8]. The infections must also be classified with respect to the frequency of recurrences. A proposed classification is into sporadic and recurrent infections [10]. Sporadic UTI is then defined as a UTI in a patient who has had less than two episodes during the previous six months and less than three S 182
episodes during the previous year. Consequently, recurrent UTI is defined as an infection in a patient with two or more episodes during the previous six months or three or more episodes during the previous year. Recurrent infections should be separated into reinfections and relapses, that is, infections caused by a new strain or by the same strain as the one causing the previous infection, respectively. If a recurrence is caused by the same species, the definition of relapse or reinfection requires biotyping or serotyping. This classification does not include chronic infections; chronic pyelonephritis is not an infection per se even if it often leads to infection. Another term which should be avoided is acute UTI, since a recurrent infection can be as acute as a sporadic one. Finally, in this context UFI must be classified as being uncomplicated or complicated. The problem here is to define which factors should be included as complications. There is general agreement that anatomical malformations, foreign bodies (including stones and catheters) and malignancies in the urinary tract result in an increased risk of acquiring bacteriuria. This is probably also true for diabetes mellitus. A consensus seems to exist that uncomplicated UTI can only occur in women [2]. Thus, any LrFI in a man should be regarded as complicated and, consequently, bacterial prostatitis becomes a complicating factor. It is, however, doubtful whether men with prostatitis should be allowed to enter U]?I trials, since the underlying condition requires long-term treatment (three weeks or more). Diseases which increase the risk of a complicated course of a UI7 rather than an increased risk of acquiring bacteriuria, e.g. malignant hypertension and immunosuppression, should be considered when definitions are decided upon.
Patient Selection
Type of Infection Infections that may require different durations of treatment should preferably not be included in the same trial. In particular, women with uncomplicated cystitis (recurrent and sporadic) should not be included in the same trial as patients with pyelonephritis or complicated infections. Since there is no consensus as to whether patients with ABU should be treated or not, such patients should also be excluded and studied separately. This leaves four types of infections to be studied: uncomplicated cystitis in women, complicated UTI (upper or lower), uncomplicated pyelonephritis and ABU. Due to limited access to patients it has been common to mix complicated infections and uncomplicated pyelonephritis. However, since the prognosis for the long-term eradication of the pathogens is much worse for those with complications, these two types of infection preferably should be studied separately. If that is not possible, prospective stratification should be considered (see below).
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Selection of the Patient Sample The main purpose of any clinical trial is to demonstrate in a small patient sample results that can be extrapolated to the population from which the sample was drawn. To achieve the highest possible external validity of the results generated, it is of crucial importance (i) that the population from which the sample is drawn is well defined and (ii) that patients entering the trial are representative for the population from which they were drawn. The second goal can be achieved in two ways: the patients can enter the trial consecutively, i.e. all available patients are included, or patients not entered can be characterized. Since true consecutiveness is obviously impossible to achieve unless ethical rules for informed consent are disregarded, the second possibility should be used and all patients who are eligible for the trial but not included should be listed in a reject log. Such a log gives the basic characteristics of the patients and reasons why each patient was not included, such as fulfillment of an exclusion criterion, refusal or administrative reasons. It allows a .comparison of patients not entered with those randomized. If, at the end of the trial, no major differences are demonstrated, it can be assumed that the sample was representative of the population.
Size of the Patient Sample The most common error in the design o f clinical trials of antibiotics is to include so few patients that the probability of demonstrating a difference becomes remote. Thus, Fihn and Stature [2] in a review of 62 controlled UTI trials found that only 21% of the trials fulfilled the rather modest aim that they demonstrate that the likelihood of a true difference of 15% in efficacy between treatment groups was less than 50%. Several factors influence the sample size. To start with, a null hypothesis must be formulated for the trial, for example that the frequency of eradication of bacteriuria with drug A does not differ more than X%- units (note the difference between % and %-units) from that obtained with drug B. The number of patients needed for testing this hypothesis depends on the type I (alpha) error, the type II (beta) error, the delta (the difference to be demonstrated) and the efficacy in the control group. The type I error, which is synonymous with the level of significance, describes the risk of falsely rejecting the null hypothesis, that is, although a difference larger than the one in the null hypothesis was found, there is not a true difference. Normally, the type I error is arbitrarily set at 0.05 and we accept a risk of 5% that a demonstrated difference is not true. The type I error is a serious one, especially in a trial which is pivotal and even more so if the end-point used is one of considerable clinical importance, for example death. If in such a trial the null hypothesis is rejected, it can normally not be repeated for ethical reasons. In such studies a lower type I error, for example 0.01, should therefore be considered. The type II error describes the risk that a null hypothesis is Infection 20 (1992) Suppl. 3
Table 1: Number of patients required to test the null hypothesis using a chi-square test without Yates' corrections; variations due to efficacy in the control group, type II (13)error and delta (difference between groups to be demonstrated). Data from [111.
95% 95% 95% 95% 90% 90% 90% 90% 80% 80% 80% 80% 70% 60% 50%
0,05 0.05 0.05 0.05 0,05 0.05 0.05 0.05 0.05 0.05 0.05 0.05 0.05 0,05 0.05
0.1 0.2 0.1 0.2 0.1 0.2 0.1 0.2 0.1 0.2 0.1 0.2 0.2 0.2 0.2
10% 10% 15% 15% 10% 10% 15% 15% 10% 10% 15% 15% 10% 10% 10%
190 135 100 75 270 200 125 100 400 295 185 135 365 395 400
falsely accepted, i.e. that although a difference was not demonstrated, it does exist. Normally the type II error is set at 20% and we thus accept a 20% risk that a true difference exists. This is sometimes expressed as the statistical power, (l-J3) x 100, that is, 80% if 13is 0.2. If, as is often the case in UTI studies, the main purpose of a trial is to show "equality" and accept the null hypothesis, the use of a lower type II error should be considered, for example 0.1 or 0.05, and compensated with an increase of the type I error to 0.1. The delta should be decided by the investigators, not by the statistician, and be based on considerations about how great a difference in efficacy between two treatments would be clinically important to demonstrate. For uncomplicated cystitis a delta larger than 10%-units should not be accepted, while a delta of 15%-units may be used in studies in patients with pyelonephritis. As shown in Table 1, all of these factors will greatly influence the sample size. Two common situations can be used as examples. In the treatment of uncomplicated cystitis, the elimination of bacteriuria is normally obtained in > 90% of patients treated if the treatment time is --> 3 days and if urine cultures taken three to nine days after completion of treatment are used as the end point. If one wants to demonstrate that the difference between two treatments is not more than 10%-units (that is, the efficacy of the test drug is allowed to vary between 80 and 100% and we still accept the null hypothesis) with a type I error of 0.05 and a type II error of 0.2, about 200 patients will be required in each group if a chi-square test is used. If the same null hypothesis is tested in patients with complicated UTI (where the efficacy rate in the control treatment can be estimated to be 50% for a late four to six week posttreatment) follow-up urine
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S. IL Norrby: Clinical Trials in UTI Table 2: Exclusions before and after randomization of patients in a trial comparing seven days treatment with norfloxacin 200 mg b.i.d., norfloxacin 400 mg b.i.d, or co-trimoxazole b.i.d. Data from [10],
No. of patients screened No. of patients excluded before randomization Reasons for exclusionbefore randomization (%) Refusal to participate Administrative reasons Previous entry into the trial History of hypersensitivity Preliminary tJI'I diagnosis changed Age below 18 years Antibiotic treatment within 72 h Concomitant treatment with drugs interacting with trial drugs Other reasons No. of patients randomized No. of patients analyzed for safety No. of patients analyzed for bacteriologicalefficacy Reasons for exclusionsfrom efficacyanalysis (%) No significantbacteriuria Treatment time too short Comcomitant antibiotic treatment Asymptomatic bacteriuria No follow-updata Other reasons
2,255 1,369 33 18 15 13 8 6 3 2 2 886 876 633 88 6 5 5 5 1
culture is used as the end-point and the number of patients per group increases to about 400. In addition to the above calculations of the patients' sample needed to test the null hypothesis, exclusions of patients before and after randomization must be taken into account in the planning of a clinical trial. Exclusions before randomization include patients who fulfil exclusion criteria, who do not provide consent or who cannot be entered for administrative reasons, for example because they cannot comply with rules for follow-up visits or because of a lack of investigational staff. Studies which have inflexible rules for follow-up visits, e.g. that they should be performed on a specific day, will lose many patients before randomization. Exclusions after randomization depend on the protocol rules for evaluability; the stricter they are, the more patients will be excluded from the final analysis of efficacy. An example of these exclusions in a UTI trial is given in Table 2. From these considerations it follows that, using an end-point such as the eradication of bacteriuria, large numbers of patients are required in each study group to test the null hypothesis with reasonable statistical power. Therefore studies on UTI as a rule must involve several centres to allow the trial to be concluded within a reasonable amount of time.
Inclusion and Exclusion Criteria The inclusion criteria used are positive ones, e.g. female sex, age > 18 years and symptoms of uncomplicated cystitis (defined). Normally these criteria are self-evident S 184
from the purpose of the study. Exclusion criteria, on the other hand, often present problems in that they tend to become too numerous. It is essential to remember that all exclusion criteria used in a trial will ultimately reduce the external validity of the results generated. For example, if patients are excluded because they are above a certain age, or use certain medications or suffer from underlying diseases, the results are valid only for individuals who do not fulfil the criteria. If exclusions such as impaired renal or hepatic function are used, impairments must be defined. Escape clauses such as "any patient who in the judgement of the investigator is not suitable for the trial" should be avoided. A special problem is the handling of patients who have bacteriuria caused by organisms resistant to one or more of the study drugs. In most studies treatment is started empirically, that is, before the results of cultures and sensitivity testing become available. In patients with cystitis, it is recommended that treatment continue even if the causative organism is reported as being resistant to one or more of the trial drugs. In such cases treatment will be discontinued if there is a clinical failure. In patients with pyelonephritis, which should be looked upon as a systemic infection with a risk of septicaemia, treatment will have to be interrupted if resistance is reported.
Study Design Controls With very few exceptions, clinical trials of antibiotics should be controlled. Uncontrolled trials are of value only if the purpose is to study pharmacokinetics or other basic aspects of the drug. The control should be prospective and tested in parallel with the test drug; historical controls or data-base controls should be avoided. The choice of control drug varies with the type of infection study and the purpose of the trial. A main rule is that the control treatment must be documented in the literature. If that is not the case, it becomes impossible to calculate the number of patients needed in the trial since that number is highly dependent on the expected efficacy in the Control group. Similarly, if the purpose of the trial is to study treatment times one has to chose a control which is documented, be it with the same drug as the one tested or another drug. For such trials, the comparisons must be made between two or more different antibiotics used for the same treatment times or with the same antibiotic used for two or more treatment times; comparisons of one antibiotic used for one treatment time and another antibiotic used for a different treatment time are not valid [12]. The control drug which leads to the quickest and smallest trim is placebo. In the treatment of symptomatic UI'I the use of placebo can hardly be regarded as ethical and an active control must be chosen. In studies of treatment of asymptomatic UTI or prophylaxis, on the other hand, the use of placebo is often medically and ethically justified.
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Randomization Randomization is the random allocation of patients to two or more treatments. Normally it is done by computer-generated random lists. It is important to note that date of birth, "every other patient," hospital admission number or similar techniques are not proper ways of randomizing patients. If a study is not double-blind, randomization should be central, that is, when a patient has been found eligible for a trial and has provided informed consent, the investigator contacts an independent randomization centre, identifies the patient and gets the allocation to treatment. This procedure guarantees that investigators' bias does not lead to misallocations.
choosing an open design are administrative ones, such as when injectable antibiotics are used for the treatment of pyelonephritis, and a high likelihood of compliance problems caused by the use of double-dummies (see above). If an open design is chosen, two requirements must be met: (i) there must be a blinded evaluator who is independent and who makes all assessments as to safety and efficacy, and (ii) the end-points used must be as objective as possible [12]. The possibilities for using objective end-points are good in l ~ I trials since bacteriuria is normally the primary end-point. However, in open trials, evaluation of clinical efficacy and adverse effects (other than laboratory results) becomes exceedingly difficult.
Stratification
Procedures before, during and after Treatment
The aim of stratification is to achieve a balance between treatment groups with regard to risk factors which are known or suspected to influence the outcome of treatment. Stratification can be made prospectively or retrospectively. Prospective stratification should be considered when the trial groups are small (< 100 patients); if the trial groups are large, chance is likely to give an even balance. It should be limited to a maximum of three strata which gives eight different arms to be analysed in each group. Retrospective stratification is an alternative to prospective stratification and implies that when the data are analysed, risk factors, if not balanced between groups, are weighed.
Characterization of Patients Entered
Blinding A trial can be double-blind (neither the patient, nor the investigator knows what treatment is given), single-blind (either the patient or the investigator is blinded), evaluator-blind (an independent person who analyses the data is blinded as to treatment given) or open. Completely open design should be avoided since it must be assumed that the investigators are biased in favour of one of the treatments studied. This is often not recognized or accepted by the investigators. However, one must then ask why an investigator agrees to participate in a trial if he or she does not believe and want to prove that one treatment is better than the other. In UTI trials treatment is often oral and it is then easy to perform double-blind trials. The usual way to achieve blinding is to use the double-dummy technique, that is, the patient receives active drug plus placebo identical to the comparator(s) a t each administration. A prerequisite for this method is that the number of tablets administered at each dose is reasonable; if it becomes too high, compliance will suffer. It is also important in a double-blind trial to achieve effective blinding not only with regard to appearance but also to taste; several antibiotics have a bitter taste which will be detected by the patients. Open design must often be used on account of specific side-effects of one of the trial drugs. Other reasons for
All patients entered in a trial must be carefully characterized with respect to previous history of UTI (including childhood infections), types of infections and frequencies. Possible complicating factors should be inquired about and, if suspected, verified. Clinical symptoms must be recorded.
Pretreatment Urine Cultures Urine cultures should be obtained pretreatment. The technique used for collecting the samples and for culture and quantitation, speciation and susceptibility determination must be described in the trial protocol. If the initial antibiotic sensitivity is performed by the disc diffusion technique, it is recommended that the strains are saved for later MIC studies. Saving of the strains will also allow the differentiation of relapses and reinfections, should the patient have a recurrent infection with the same species after treatment.
Other Pretreatment Laboratory Samples If one of the antibiotics studied is not licensed, rather extensive biochemical and haematological procedures are normally required for regulatory purposes and for the monitoring of safety. Methods that may assist in the differential diagnosis of cystitis and pyelonephritis are C-reactive protein (CRP) determinations and urinalysis (including microscopy).
Treatment In most trials, treatment is given either by mouth or parenterally. In the latter case antibiotic trials tend to be artificial when compared with the way in which treatment is given in a patient who is not part of a clinical trial. For example a patient admitted to hospital because of pyelonephritis is often treated with an injectable antibiotic for one to two days and treatment is then changed to an oral drug. In a trial, however, the whole course if normally
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given with the injectable antibiotic. It seems clear that such trials have little validity for the actual use of antibiotics. Instead, studies in which treatment is started parenterally and continued orally should be considered. In such studies, the criteria for when the switch to oral treatment should take place must be defined and be as objective as possible. If such a design is used, an obvious difficulty is that most modern broad-spectrum injectable antibiotics are not available for oral administration. In such cases the oral follow-up treatment should be chosen carefully and preferably be the same in all treatment groups. This section of the protocol must also contain clear rules about how many doses can be missed without a patient having to be excluded from full evaluability. The minimum treatment time must be decided.
pyelonephritis, a verification of the diagnosis can be obtained by subcutaneous (not intranasal) challenge with an antidiuretic hormone, followed by assay of the urine osmolarity. The time for the first posttreatment urine sample varies with the half-life of the drugs tested. The main rule is that the urine should have been completely free from antibiotics for at least 24 h before the sample is obtained. This means that it cannot be taken earlier than three days after the last dose if one of the trial drugs is a [3-1actam and not earlier than five days posttreatment if cotrimoxazole or a fluoro-quinotone is used. The majority of all UTI studies include an early follow-up but relatively few aim at studying the results four to six weeks post treatment. Such samples should be obtained in as many patients as possible but the late efficacy should not be the primary end-point for the trial.
Procedures during Treatment Extra visits during treatment are of limited value. Few patients have positive urine cultures and the only benefit is that an extra visit offers a possibility of monitoring compliance by the demonstration of antibacterial activity in the urine. The duration of clinical symptoms is most easily registered by diary cards on which the patients record the presence or absence of defined symptoms such as frequency, dysuria and fever. All types of grading of symptoms should be avoided since they are highly subjective.
Treatment Time The treatment time is well documented for uncomplicated cystitis [13]; single doses always give lower rates of elimination of bacteriuria than treatment for --- 3 days. With cotrimoxazole, it has been clearly shown that nothing is gained by prolonging the treatment time to --> 5 days, while significant differences in favour of longer treatment times have been shown for 13-1actam antibiotics [13]. However, for any new antibiotic to be used in UTI, the optimal treatment time •must be documented; extrapolation from one drug to another can only be allowed for drugs which are almost identical in their microbiological and pharmacokinetic characteristics. In pyelonephritis, few studies on the optimal treatment time have been performed but 14 days seem to be required [14].
Compliance Control The routine technique for compliance control is by pill count at the first follow-up visit at which time the patient is also interviewed as to compliance. In addition, analysis of antibacterial activity in the urine may be considered (see above).
Posttreatment Follow-Up Biochemical and haematological tests may be required for regulatory purposes. If the study includes patients with S 186
Analysis of Efficacy General Rules Criteria for analysability ("evaluability") must be defined in the study protocol. All analyses to be performed in a clinical trial should also be outlined in the study protocol. When the study is completed, decisions must be taken as to which analyses are to be performed. These decisions should be made before the patients are grouped and especially before the randomization code is broken. ,amalyses performed after breakage of the code have much less value and the results should, in principle, only be used to indicate further prospective trials. Interim analyses should be avoided in most UTI trials. First, they may introduce a risk of unnecessary bias for or against one of the drugs studied. Secondly, with each interim analysis including a significance test, the number of patients required to test the null hypothesis will increase to compensate for the risk of mass significance.
Clinical Efficacy A considerable proportion of LrrI studies has not included an analysis of the clinical efficacy [2]. It seems quite clear that both clinical and bacteriological efficacy must be assessed. The clinical efficacy evaluation should be made both according to the intention-to-treat principle and in patients fulfilling criteria for full analysability. In the former analysis, which is also called a pragmatic analysis, all patients randomized for whom data are available are analysed for efficacy. A therapeutic failure is then not only a patient who despite treatment had persisting symptoms, but also a patient who for any reason did not complete the treatment course, for example one who discontinued treatment due to adverse reactions or who died. In this analysis patients who were misallocated are analysed in the group they should have belonged to. The main aim of the intention-to-treat analysis is to simulate the clinical situation where a drug is prescribed and the patient is
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Table 3: Quality check list for published UTI trials. A trial of reasonable quality must yield a minimum number of "no" answers.
patients w h o fulfil certain preset criteria, for example that t r e a t m e n t should have b e e n taken for a m i n i m u m time and that bacteriuria should have b e e n proven.
Introduction
* Was the efficacy of the control treatment documented by references? * Was the treatment time documented for the control treatment? Material and Methods
* Were major terms defined? * Did the patients have similar types of LrFI? * Was the null hypothesis given and the size of the patient sample adequately motivated with type I and II errors, delta and expected efficacy in the control group? * Were inclusion and exclusion criteriadescribed? * Did exclusion criteria limit the external validity of the results? * Was the study controlled and properly randomized? * Was the study double-blind? * If the study was open or single-blind, was central randomization used? * Was a reject log used for patients excluded before randomization? * Were microbiological procedures described? * Were criteria for analysability defined?
Bacteriological Efficacy In a U T I trial bacteriological efficacy is often the main end-point. It should be analysed b o t h at early and late follow-up. A p r o b l e m arises in the handling of d a t a g e n e r a t e d at the late follow-up, since patients w h o w e r e failures at the early follow-up are automatically excluded f r o m the late follow-up. As a result, a drug with p o o r efficacy at the early follow-up m a y a p p e a r better at the late follow-up. T o some extent this can be solved by analysing a c c u m u l a t e d efficacy, that is, the most negative o u t c o m e of both follow-ups [11]. Such an analysis also solves the problems o f patients w h o fail to r e p o r t for one o f the two follow-ups. T h e analysis o f bacteriological efficacy should be correlated to the one of clinical efficacy and vice versa.
Results
* Was the study sample representative for the population from which it was drawn? * Were risk factors identified and described? * Was clinical efficacy studied? * Was an intention-to-treat analysis performed? * Were data given for all patients randomized and reasons for exclusions after randomization described? * Were less than 5% of randomized patients lost to follow-up? * Were both early and late follow-ups of elimination of bacteriuria performed? * Was the early follow-up sufficiently late after the last dose to allow for at least 24 h of antibiotic-free urine? * Were reinfections and relapses differentiated by biotyping or serotyping in patients with recurrences caused by the original species? * Were bacteriological and clinical results correlated to each other and to susceptibilities to the antibiotics studied? Discussion and Conclusions
* If the null hypothesis was accepted, was the power of the study at least 80%? * Were differences between treatment efficacies, if demonstrated, likely to have been due to factors other than resistance of the causative organisms? * Can the results of the trial be extrapolated to a larger population?
expected to take it and r e s p o n d to it. A secondary aim is to detect biases of the investigators which are otherwise not obvious. T h e s e c o n d analysis o f clinical efficacy is p e r f o r m e d in
Conclusions
U T I is an extremely c o m m o n type of infection. Most cases are uncomplicated and easily treated with antibiotics. D u e to the high incidence o f UTI, even a relatively small miscalculation of the efficacy o f an antibiotic will affect a major g r o u p of patients if the drug b e c o m e s c o m m o n l y used for U T I treatment. Against this b a c k g r o u n d it seems p r u d e n t to d e m a n d a high quality of clinical trials in U T I patients. Studies including 30-40 patients in each group, finding no significant differences a n d concluding with a statement that the treatments w e r e "equally g o o d " no longer deserve to be published or p r e s e n t e d at scientific meetings. However, improved quality also means that U T I trials must in most cases include several centres. I n turn, it follows that the academic credits for the individual investigator b e c o m e minimal; often she o r he is r e d u c e d to a m e n t i o n in a f o o t n o t e of a study g r o u p publication. T h e only way to r e d u c e this p r o b l e m is to e n c o u r a g e subprojects which can be published independently. Such subprojects m a y be in microbiology, basic pathogenesis, pharmacokinetics or specialised safety analyses - all fields which are by no m e a n s p r e e m p t e d . T a b l e 3 is a suggestion for a list of questions which m a y be asked in each U T I study in o r d e r to ensure that basic quality requirements are fulfilled.
References
1. Norrby, R.: Quality of antibiotic clinical trials. J. Antimicrob. Chemother. 14 (1984) 205-208. 2. Fihn, S. D., Stature, W. E.: Interpretation and comparison of treatment studies for uncomplicated urinary tract infections in women. Rev. Infect. Dis. 7 (1985) 468--478. 3. Ronald, A. R.: Clinical trials of antimicrobial agents following licensure. J. Infect. Dis. 159 (1989) 3--6.
4. Working Party of the British Society for Antimicrobial Chemotherapy: The clinical evaluation of antibacterial drugs. J. Antimicrob. Chemother. 23 (Suppl. B) (1989) 1--42. 5. Finch, R. G.: The clinical evaluation of antibacterial drugs: Guidelines of the British Society for Antimicrobial Chemotherapy. Eur. J. Clin. Microbiol. Infect. Dis. 9 (1990) 542-547. 6. Gilbert, D. N., Beam, T. R., Kunin, C. M.: The implications for
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7. 8.
9. I0.
Europe of revised FDA guidelines for clinical trials of anti-infective agents. Eur. J. Clin. Microbiol. Infect. Dis. 9 (1990) 552-558. Lunde, L: Guidelines of the World Health Organization for clinical trials of antimicrobial agents. Enr. J. Clin. Microbiol. Infect. Dis. 9 (1990) 548-55t. Kass, E. H.: Asymptomatic infections in the urinary tract. Trans. Assoc. Am. Physicians 69 (1956) 56--63. Stamm, W. E., Counts, G. W., Running, K. IL, Fihn, S., Turek, M., Holmes, K. IL: Diagnosis of coliform infection in acutely dysuric women. N. Engl. J. Med. 307 (1982) 463--468. Urinary Tract Infection Study Group: Coordinated multicenter study of norfloxacin versus trimethoprim-sulfamethoxazole treatment of symptomatic urinary tract infections.J. Infect. Dis. 155 (1987) 170-177.
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11. Huitfeldt, B.: Statistical aspects of clinical trials of antibiotics in acute infections. Rev, Infect. Dis. 8 (Suppl. 3) (1986) $350-$357. 12. Byar, D. P., Sehoenfeld, D. A., Green, S. B., Amato, D. A., Davis, R., De Gruttola, V., Finkelstein, D. M., Gatsonis, C., Gelber, R. D., Lagakos, S., Letkopoulo, M., Tsiatis, A. A., Selen, M., Peto, J., Freedman, L S., Gall, M., Simon, R., Eilenberg, S. S., Collins, IL, Peto, IL, Peto, I?.: Design considerations for AIDS trials. N. Engl. J. Med. 323 (1990) 1343- 1348. 13. Norrby, S. R.: Short-term treatment of uncomplicated urinary tract infections in women. Rev. Infect. Dis. 12 (1990) 458-467. 14. Norrby, S. R.: Efficacy and safety of antibiotic treatment in relation to treatment time. Scan& J. Infect. Dis. (in press).
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Design of Clinical Trials in Patients with Urinary Tract Infections Summary: This overview deals with the optimization of the design of clinical trials in patients with urinary tract infections (LrFIs). Despite the fact that LrFI is one of the most common types of infection and that the main end-point (elimination or persistence ~of bacteriuria) is objective and easy to register, the quality of studies performed and published has generally been less than optimal. Problems that should always be addressed in the study protocol are definitions of terms used, for example bacteriuria, level of the infection (cystitis or pyelonephritis), and uncomplicated and complicated infections; dimension of the patient's sample to allow adequate testing of a null hypothesis; procedures before, during and after treatment; methods for analysis of the results. Zusammenfassung: Studiendesi..gn bei Patienten mit Harnwegsinfektionen. In diesem Uberblick wird die Optimierung klinischer Studien bei Harnwegsinfektionen (HWI) dargestellt. Obwohl HWI zu den h/iufigsten Infektionskrankheiten gehfren und der Endpunkt (Eliminierung'oder Persistenz der Bakteriurie) objektiv und leicht festzustellen ist, zeigt sich, dab die Qualit/it der durchgefiihrten und publizierten Studien im allgemeinen nicht optimal ist. Es ist wichtig, dab in allen Studienprotokollen folgende Gesichtspunkte beriicksichtigt werden: Definition der verwendeten Begriffe, z. B. Bakteriurie, Ebene der Infektion (Zystitis oder Pyelonephritis) sowie unkomplizierte und komplizierte Infektion; der Umfang der Patientenstichprobe, um die Nullhypothese ausreichend zu testen; MaBnahmen vor, w/ihrend und nach der Therapie; Methoden zur Analyse der Ergebnisse.
Introduction Antimicrobial agents differ from other types of drug in that they ideally have no effect on the host; any such effect is a potential adverse reaction. Instead, they interact with the pathogens that cause infection. Thus, the pharmacodynamics of antimicrobial agents are the interactions between the drug and the microbe, not between the drug and the host. From these interactions follows a potential risk of ecological side-effects caused by unwanted disturbances of the normal microbial flora of the patient treated. Clinical trials of antimicrobial agents have tended to be of generally low quality [1-3]. There are several reasons for this; (I) the end-points used are often dichotomous, i.e. outcome is expressed in terms such as cured versus improved or bacterial eradication versus bacterial
persistence, necessitating very large patient samples, (II) factors other than the infection itself, e.g. underlying diseases or immunodeficiencies, influence the outcome of treatment and make the evaluation of the effects of the drug per se difficult, (III) end-points are often subjective rather than objective, and (IV) medical interventions other than drug treatment, such as surgical drainage of purulent infections, are often critical for the cure of an infection. Despite the fact that, for reasons discussed below, urinary tract infections (UTIs) are among the easier types of infection to study, the quality of the majority of UTI trials has also been low [2]. In the following discussion about the design of clinical trials in patients with UTI, it is important to realize that UTI constitutes a group of infections which vary considerably with regard to treatment, duration and prognosis. Extrapolation of results obtained in one type of UTI to another type is therefore not normally possible. This overview will not deal with registration and analysis of safety, nor with ethical aspects since in that context UTI does not differ from other infections.
Guidelines for Clinical Trial Design General guidelines for the design of clinical trials of antimicrobial agents have been published by the British Society for Antimicrobial Chemotherapy (BSAC) [4,5]. Such guidelines, as well as specific ones, have been published by the Infectious Diseases Society of America (IDSA) under contract with the U.S. Food and Drug Administration (FDA)[6]. The World Health Organization is also in the process of publishing guidelines for trials of antimicrobials [7]. The IDSA/FDA document includes specific guidelines for several types of infections, including UTI. Efforts are in progress to use the IDSA/FDA guidelines as a format for a European counterpart. This would allow a greater degree of cooperation between US and European investigators and eliminate some of the repetitive studies now being performed on both sides of the Atlantic. Finally, there are several documents regulating Good Clinical Practice (GCP) for clinical trials, that is, the general requirements for the conduct of clinical trials with regard to relations between the pharmaceutical industry and investigators monitoring the trials etc. [7].
Definitions In all clinical trials, the terminology used must be clear and defined. Internationally acceptable definitions are preferable. However, such definitions are often lacking S. R. Norrby, M. D., Ph.D., Dept. of InfectiousDiseases,Lund University Hospital, S-22185 Lund, Sweden.
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S. R. Norrby: Clinical Trials in UTI and must then be agreed before the trial is started, and included in the study protocol. For IYFI, the following definitions are proposed: Significant bacteriuria can be defined in several ways. Kass [8] in his classical study defined it as -> 105 colony-forming units (cfu) per ml of a midstream urine sample or any bacterial count in a sample obtained by bladder puncture. Stature et al. [9] found that, in midstream urine samples, UTI defined as bacterial counts of -> 10z cfu/ml gave the highest specificity and sensitivity. However, if these lower counts are accepted, it is important to realize that sampling procedures must be optimized and the samples be kept refrigerated during the entire interval between micturation and inoculation at the laboratory. It should be noted that studies on the break-points for significant bacteriuria have concentrated on gram-negative organisms. In infections caused by Staphylococcus saprophyticus and possibly also other staphylococci, a lower break-point should be used, since these organisms clump together and each colony represents many organisms. In this respect it is also important to decide beforehand how samples yielding more than one bacterial species should be interpreted. In patients with bladder catheters two or even three strains may be present in the urine. Patients who are not catheterized and who have symptomatic infections, on the other hand, normally have only a single strain in their urine and samples yielding two or more strains should be regarded as contaminated. The classification of UTIs by the level of the urinary tract affected into cystitis (lower) and pyelonephritis (upper) seems simple but is often very difficult in clinical practice. The typical symptoms of pyelonephritis, fever and loin pain, may be masked by the intake of analgesics, which often also act as antipyretics. Laboratory tests, for example the measurement of C-reactive protein (CRP), presence or absence of casts by urine microscopy, and reduced urine osmolarity following challenge with antidiuretic hormone, may assist in the diagnosis. The value of testing for the presence in urine of antibody-coated bacteria (ACB) is more doubtful. This test has either a low specificity or a low sensitivity, depending on which frequency of ACB-positivity is chosen as indicative of pyelonephritis. In protocols for trials that include patients with pyelonephritis, the diagnostic criteria must be clearly defined. In both pyelonephritis and cystitis, the prognosis varies according to the type of infection. The infections must be classified as being symptomatic or a.~mptomatic. Asymptomatic infections include asymptomatic bacteriuria (ABU) for which the diagnostic criteria are stricter than for symptomatic infections (at least two midstream urine samples are required) [8]. The infections must also be classified with respect to the frequency of recurrences. A proposed classification is into sporadic and recurrent infections [10]. Sporadic UTI is then defined as a UTI in a patient who has had less than two episodes during the previous six months and less than three S 182
episodes during the previous year. Consequently, recurrent UTI is defined as an infection in a patient with two or more episodes during the previous six months or three or more episodes during the previous year. Recurrent infections should be separated into reinfections and relapses, that is, infections caused by a new strain or by the same strain as the one causing the previous infection, respectively. If a recurrence is caused by the same species, the definition of relapse or reinfection requires biotyping or serotyping. This classification does not include chronic infections; chronic pyelonephritis is not an infection per se even if it often leads to infection. Another term which should be avoided is acute UTI, since a recurrent infection can be as acute as a sporadic one. Finally, in this context UFI must be classified as being uncomplicated or complicated. The problem here is to define which factors should be included as complications. There is general agreement that anatomical malformations, foreign bodies (including stones and catheters) and malignancies in the urinary tract result in an increased risk of acquiring bacteriuria. This is probably also true for diabetes mellitus. A consensus seems to exist that uncomplicated UTI can only occur in women [2]. Thus, any LrFI in a man should be regarded as complicated and, consequently, bacterial prostatitis becomes a complicating factor. It is, however, doubtful whether men with prostatitis should be allowed to enter U]?I trials, since the underlying condition requires long-term treatment (three weeks or more). Diseases which increase the risk of a complicated course of a UI7 rather than an increased risk of acquiring bacteriuria, e.g. malignant hypertension and immunosuppression, should be considered when definitions are decided upon.
Patient Selection
Type of Infection Infections that may require different durations of treatment should preferably not be included in the same trial. In particular, women with uncomplicated cystitis (recurrent and sporadic) should not be included in the same trial as patients with pyelonephritis or complicated infections. Since there is no consensus as to whether patients with ABU should be treated or not, such patients should also be excluded and studied separately. This leaves four types of infections to be studied: uncomplicated cystitis in women, complicated UTI (upper or lower), uncomplicated pyelonephritis and ABU. Due to limited access to patients it has been common to mix complicated infections and uncomplicated pyelonephritis. However, since the prognosis for the long-term eradication of the pathogens is much worse for those with complications, these two types of infection preferably should be studied separately. If that is not possible, prospective stratification should be considered (see below).
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Selection of the Patient Sample The main purpose of any clinical trial is to demonstrate in a small patient sample results that can be extrapolated to the population from which the sample was drawn. To achieve the highest possible external validity of the results generated, it is of crucial importance (i) that the population from which the sample is drawn is well defined and (ii) that patients entering the trial are representative for the population from which they were drawn. The second goal can be achieved in two ways: the patients can enter the trial consecutively, i.e. all available patients are included, or patients not entered can be characterized. Since true consecutiveness is obviously impossible to achieve unless ethical rules for informed consent are disregarded, the second possibility should be used and all patients who are eligible for the trial but not included should be listed in a reject log. Such a log gives the basic characteristics of the patients and reasons why each patient was not included, such as fulfillment of an exclusion criterion, refusal or administrative reasons. It allows a .comparison of patients not entered with those randomized. If, at the end of the trial, no major differences are demonstrated, it can be assumed that the sample was representative of the population.
Size of the Patient Sample The most common error in the design o f clinical trials of antibiotics is to include so few patients that the probability of demonstrating a difference becomes remote. Thus, Fihn and Stature [2] in a review of 62 controlled UTI trials found that only 21% of the trials fulfilled the rather modest aim that they demonstrate that the likelihood of a true difference of 15% in efficacy between treatment groups was less than 50%. Several factors influence the sample size. To start with, a null hypothesis must be formulated for the trial, for example that the frequency of eradication of bacteriuria with drug A does not differ more than X%- units (note the difference between % and %-units) from that obtained with drug B. The number of patients needed for testing this hypothesis depends on the type I (alpha) error, the type II (beta) error, the delta (the difference to be demonstrated) and the efficacy in the control group. The type I error, which is synonymous with the level of significance, describes the risk of falsely rejecting the null hypothesis, that is, although a difference larger than the one in the null hypothesis was found, there is not a true difference. Normally, the type I error is arbitrarily set at 0.05 and we accept a risk of 5% that a demonstrated difference is not true. The type I error is a serious one, especially in a trial which is pivotal and even more so if the end-point used is one of considerable clinical importance, for example death. If in such a trial the null hypothesis is rejected, it can normally not be repeated for ethical reasons. In such studies a lower type I error, for example 0.01, should therefore be considered. The type II error describes the risk that a null hypothesis is Infection 20 (1992) Suppl. 3
Table 1: Number of patients required to test the null hypothesis using a chi-square test without Yates' corrections; variations due to efficacy in the control group, type II (13)error and delta (difference between groups to be demonstrated). Data from [111.
95% 95% 95% 95% 90% 90% 90% 90% 80% 80% 80% 80% 70% 60% 50%
0,05 0.05 0.05 0.05 0,05 0.05 0.05 0.05 0.05 0.05 0.05 0.05 0.05 0,05 0.05
0.1 0.2 0.1 0.2 0.1 0.2 0.1 0.2 0.1 0.2 0.1 0.2 0.2 0.2 0.2
10% 10% 15% 15% 10% 10% 15% 15% 10% 10% 15% 15% 10% 10% 10%
190 135 100 75 270 200 125 100 400 295 185 135 365 395 400
falsely accepted, i.e. that although a difference was not demonstrated, it does exist. Normally the type II error is set at 20% and we thus accept a 20% risk that a true difference exists. This is sometimes expressed as the statistical power, (l-J3) x 100, that is, 80% if 13is 0.2. If, as is often the case in UTI studies, the main purpose of a trial is to show "equality" and accept the null hypothesis, the use of a lower type II error should be considered, for example 0.1 or 0.05, and compensated with an increase of the type I error to 0.1. The delta should be decided by the investigators, not by the statistician, and be based on considerations about how great a difference in efficacy between two treatments would be clinically important to demonstrate. For uncomplicated cystitis a delta larger than 10%-units should not be accepted, while a delta of 15%-units may be used in studies in patients with pyelonephritis. As shown in Table 1, all of these factors will greatly influence the sample size. Two common situations can be used as examples. In the treatment of uncomplicated cystitis, the elimination of bacteriuria is normally obtained in > 90% of patients treated if the treatment time is --> 3 days and if urine cultures taken three to nine days after completion of treatment are used as the end point. If one wants to demonstrate that the difference between two treatments is not more than 10%-units (that is, the efficacy of the test drug is allowed to vary between 80 and 100% and we still accept the null hypothesis) with a type I error of 0.05 and a type II error of 0.2, about 200 patients will be required in each group if a chi-square test is used. If the same null hypothesis is tested in patients with complicated UTI (where the efficacy rate in the control treatment can be estimated to be 50% for a late four to six week posttreatment) follow-up urine
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S. IL Norrby: Clinical Trials in UTI Table 2: Exclusions before and after randomization of patients in a trial comparing seven days treatment with norfloxacin 200 mg b.i.d., norfloxacin 400 mg b.i.d, or co-trimoxazole b.i.d. Data from [10],
No. of patients screened No. of patients excluded before randomization Reasons for exclusionbefore randomization (%) Refusal to participate Administrative reasons Previous entry into the trial History of hypersensitivity Preliminary tJI'I diagnosis changed Age below 18 years Antibiotic treatment within 72 h Concomitant treatment with drugs interacting with trial drugs Other reasons No. of patients randomized No. of patients analyzed for safety No. of patients analyzed for bacteriologicalefficacy Reasons for exclusionsfrom efficacyanalysis (%) No significantbacteriuria Treatment time too short Comcomitant antibiotic treatment Asymptomatic bacteriuria No follow-updata Other reasons
2,255 1,369 33 18 15 13 8 6 3 2 2 886 876 633 88 6 5 5 5 1
culture is used as the end-point and the number of patients per group increases to about 400. In addition to the above calculations of the patients' sample needed to test the null hypothesis, exclusions of patients before and after randomization must be taken into account in the planning of a clinical trial. Exclusions before randomization include patients who fulfil exclusion criteria, who do not provide consent or who cannot be entered for administrative reasons, for example because they cannot comply with rules for follow-up visits or because of a lack of investigational staff. Studies which have inflexible rules for follow-up visits, e.g. that they should be performed on a specific day, will lose many patients before randomization. Exclusions after randomization depend on the protocol rules for evaluability; the stricter they are, the more patients will be excluded from the final analysis of efficacy. An example of these exclusions in a UTI trial is given in Table 2. From these considerations it follows that, using an end-point such as the eradication of bacteriuria, large numbers of patients are required in each study group to test the null hypothesis with reasonable statistical power. Therefore studies on UTI as a rule must involve several centres to allow the trial to be concluded within a reasonable amount of time.
Inclusion and Exclusion Criteria The inclusion criteria used are positive ones, e.g. female sex, age > 18 years and symptoms of uncomplicated cystitis (defined). Normally these criteria are self-evident S 184
from the purpose of the study. Exclusion criteria, on the other hand, often present problems in that they tend to become too numerous. It is essential to remember that all exclusion criteria used in a trial will ultimately reduce the external validity of the results generated. For example, if patients are excluded because they are above a certain age, or use certain medications or suffer from underlying diseases, the results are valid only for individuals who do not fulfil the criteria. If exclusions such as impaired renal or hepatic function are used, impairments must be defined. Escape clauses such as "any patient who in the judgement of the investigator is not suitable for the trial" should be avoided. A special problem is the handling of patients who have bacteriuria caused by organisms resistant to one or more of the study drugs. In most studies treatment is started empirically, that is, before the results of cultures and sensitivity testing become available. In patients with cystitis, it is recommended that treatment continue even if the causative organism is reported as being resistant to one or more of the trial drugs. In such cases treatment will be discontinued if there is a clinical failure. In patients with pyelonephritis, which should be looked upon as a systemic infection with a risk of septicaemia, treatment will have to be interrupted if resistance is reported.
Study Design Controls With very few exceptions, clinical trials of antibiotics should be controlled. Uncontrolled trials are of value only if the purpose is to study pharmacokinetics or other basic aspects of the drug. The control should be prospective and tested in parallel with the test drug; historical controls or data-base controls should be avoided. The choice of control drug varies with the type of infection study and the purpose of the trial. A main rule is that the control treatment must be documented in the literature. If that is not the case, it becomes impossible to calculate the number of patients needed in the trial since that number is highly dependent on the expected efficacy in the Control group. Similarly, if the purpose of the trial is to study treatment times one has to chose a control which is documented, be it with the same drug as the one tested or another drug. For such trials, the comparisons must be made between two or more different antibiotics used for the same treatment times or with the same antibiotic used for two or more treatment times; comparisons of one antibiotic used for one treatment time and another antibiotic used for a different treatment time are not valid [12]. The control drug which leads to the quickest and smallest trim is placebo. In the treatment of symptomatic UI'I the use of placebo can hardly be regarded as ethical and an active control must be chosen. In studies of treatment of asymptomatic UTI or prophylaxis, on the other hand, the use of placebo is often medically and ethically justified.
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Randomization Randomization is the random allocation of patients to two or more treatments. Normally it is done by computer-generated random lists. It is important to note that date of birth, "every other patient," hospital admission number or similar techniques are not proper ways of randomizing patients. If a study is not double-blind, randomization should be central, that is, when a patient has been found eligible for a trial and has provided informed consent, the investigator contacts an independent randomization centre, identifies the patient and gets the allocation to treatment. This procedure guarantees that investigators' bias does not lead to misallocations.
choosing an open design are administrative ones, such as when injectable antibiotics are used for the treatment of pyelonephritis, and a high likelihood of compliance problems caused by the use of double-dummies (see above). If an open design is chosen, two requirements must be met: (i) there must be a blinded evaluator who is independent and who makes all assessments as to safety and efficacy, and (ii) the end-points used must be as objective as possible [12]. The possibilities for using objective end-points are good in l ~ I trials since bacteriuria is normally the primary end-point. However, in open trials, evaluation of clinical efficacy and adverse effects (other than laboratory results) becomes exceedingly difficult.
Stratification
Procedures before, during and after Treatment
The aim of stratification is to achieve a balance between treatment groups with regard to risk factors which are known or suspected to influence the outcome of treatment. Stratification can be made prospectively or retrospectively. Prospective stratification should be considered when the trial groups are small (< 100 patients); if the trial groups are large, chance is likely to give an even balance. It should be limited to a maximum of three strata which gives eight different arms to be analysed in each group. Retrospective stratification is an alternative to prospective stratification and implies that when the data are analysed, risk factors, if not balanced between groups, are weighed.
Characterization of Patients Entered
Blinding A trial can be double-blind (neither the patient, nor the investigator knows what treatment is given), single-blind (either the patient or the investigator is blinded), evaluator-blind (an independent person who analyses the data is blinded as to treatment given) or open. Completely open design should be avoided since it must be assumed that the investigators are biased in favour of one of the treatments studied. This is often not recognized or accepted by the investigators. However, one must then ask why an investigator agrees to participate in a trial if he or she does not believe and want to prove that one treatment is better than the other. In UTI trials treatment is often oral and it is then easy to perform double-blind trials. The usual way to achieve blinding is to use the double-dummy technique, that is, the patient receives active drug plus placebo identical to the comparator(s) a t each administration. A prerequisite for this method is that the number of tablets administered at each dose is reasonable; if it becomes too high, compliance will suffer. It is also important in a double-blind trial to achieve effective blinding not only with regard to appearance but also to taste; several antibiotics have a bitter taste which will be detected by the patients. Open design must often be used on account of specific side-effects of one of the trial drugs. Other reasons for
All patients entered in a trial must be carefully characterized with respect to previous history of UTI (including childhood infections), types of infections and frequencies. Possible complicating factors should be inquired about and, if suspected, verified. Clinical symptoms must be recorded.
Pretreatment Urine Cultures Urine cultures should be obtained pretreatment. The technique used for collecting the samples and for culture and quantitation, speciation and susceptibility determination must be described in the trial protocol. If the initial antibiotic sensitivity is performed by the disc diffusion technique, it is recommended that the strains are saved for later MIC studies. Saving of the strains will also allow the differentiation of relapses and reinfections, should the patient have a recurrent infection with the same species after treatment.
Other Pretreatment Laboratory Samples If one of the antibiotics studied is not licensed, rather extensive biochemical and haematological procedures are normally required for regulatory purposes and for the monitoring of safety. Methods that may assist in the differential diagnosis of cystitis and pyelonephritis are C-reactive protein (CRP) determinations and urinalysis (including microscopy).
Treatment In most trials, treatment is given either by mouth or parenterally. In the latter case antibiotic trials tend to be artificial when compared with the way in which treatment is given in a patient who is not part of a clinical trial. For example a patient admitted to hospital because of pyelonephritis is often treated with an injectable antibiotic for one to two days and treatment is then changed to an oral drug. In a trial, however, the whole course if normally
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given with the injectable antibiotic. It seems clear that such trials have little validity for the actual use of antibiotics. Instead, studies in which treatment is started parenterally and continued orally should be considered. In such studies, the criteria for when the switch to oral treatment should take place must be defined and be as objective as possible. If such a design is used, an obvious difficulty is that most modern broad-spectrum injectable antibiotics are not available for oral administration. In such cases the oral follow-up treatment should be chosen carefully and preferably be the same in all treatment groups. This section of the protocol must also contain clear rules about how many doses can be missed without a patient having to be excluded from full evaluability. The minimum treatment time must be decided.
pyelonephritis, a verification of the diagnosis can be obtained by subcutaneous (not intranasal) challenge with an antidiuretic hormone, followed by assay of the urine osmolarity. The time for the first posttreatment urine sample varies with the half-life of the drugs tested. The main rule is that the urine should have been completely free from antibiotics for at least 24 h before the sample is obtained. This means that it cannot be taken earlier than three days after the last dose if one of the trial drugs is a [3-1actam and not earlier than five days posttreatment if cotrimoxazole or a fluoro-quinotone is used. The majority of all UTI studies include an early follow-up but relatively few aim at studying the results four to six weeks post treatment. Such samples should be obtained in as many patients as possible but the late efficacy should not be the primary end-point for the trial.
Procedures during Treatment Extra visits during treatment are of limited value. Few patients have positive urine cultures and the only benefit is that an extra visit offers a possibility of monitoring compliance by the demonstration of antibacterial activity in the urine. The duration of clinical symptoms is most easily registered by diary cards on which the patients record the presence or absence of defined symptoms such as frequency, dysuria and fever. All types of grading of symptoms should be avoided since they are highly subjective.
Treatment Time The treatment time is well documented for uncomplicated cystitis [13]; single doses always give lower rates of elimination of bacteriuria than treatment for --- 3 days. With cotrimoxazole, it has been clearly shown that nothing is gained by prolonging the treatment time to --> 5 days, while significant differences in favour of longer treatment times have been shown for 13-1actam antibiotics [13]. However, for any new antibiotic to be used in UTI, the optimal treatment time •must be documented; extrapolation from one drug to another can only be allowed for drugs which are almost identical in their microbiological and pharmacokinetic characteristics. In pyelonephritis, few studies on the optimal treatment time have been performed but 14 days seem to be required [14].
Compliance Control The routine technique for compliance control is by pill count at the first follow-up visit at which time the patient is also interviewed as to compliance. In addition, analysis of antibacterial activity in the urine may be considered (see above).
Posttreatment Follow-Up Biochemical and haematological tests may be required for regulatory purposes. If the study includes patients with S 186
Analysis of Efficacy General Rules Criteria for analysability ("evaluability") must be defined in the study protocol. All analyses to be performed in a clinical trial should also be outlined in the study protocol. When the study is completed, decisions must be taken as to which analyses are to be performed. These decisions should be made before the patients are grouped and especially before the randomization code is broken. ,amalyses performed after breakage of the code have much less value and the results should, in principle, only be used to indicate further prospective trials. Interim analyses should be avoided in most UTI trials. First, they may introduce a risk of unnecessary bias for or against one of the drugs studied. Secondly, with each interim analysis including a significance test, the number of patients required to test the null hypothesis will increase to compensate for the risk of mass significance.
Clinical Efficacy A considerable proportion of LrrI studies has not included an analysis of the clinical efficacy [2]. It seems quite clear that both clinical and bacteriological efficacy must be assessed. The clinical efficacy evaluation should be made both according to the intention-to-treat principle and in patients fulfilling criteria for full analysability. In the former analysis, which is also called a pragmatic analysis, all patients randomized for whom data are available are analysed for efficacy. A therapeutic failure is then not only a patient who despite treatment had persisting symptoms, but also a patient who for any reason did not complete the treatment course, for example one who discontinued treatment due to adverse reactions or who died. In this analysis patients who were misallocated are analysed in the group they should have belonged to. The main aim of the intention-to-treat analysis is to simulate the clinical situation where a drug is prescribed and the patient is
Infection 20 (1992) Suppl. 3 © MMV Medizin Verlag GmbH Mtinchen, Miinchen 1992
S. R. Norrby: Clinical Trials in UTI
Table 3: Quality check list for published UTI trials. A trial of reasonable quality must yield a minimum number of "no" answers.
patients w h o fulfil certain preset criteria, for example that t r e a t m e n t should have b e e n taken for a m i n i m u m time and that bacteriuria should have b e e n proven.
Introduction
* Was the efficacy of the control treatment documented by references? * Was the treatment time documented for the control treatment? Material and Methods
* Were major terms defined? * Did the patients have similar types of LrFI? * Was the null hypothesis given and the size of the patient sample adequately motivated with type I and II errors, delta and expected efficacy in the control group? * Were inclusion and exclusion criteriadescribed? * Did exclusion criteria limit the external validity of the results? * Was the study controlled and properly randomized? * Was the study double-blind? * If the study was open or single-blind, was central randomization used? * Was a reject log used for patients excluded before randomization? * Were microbiological procedures described? * Were criteria for analysability defined?
Bacteriological Efficacy In a U T I trial bacteriological efficacy is often the main end-point. It should be analysed b o t h at early and late follow-up. A p r o b l e m arises in the handling of d a t a g e n e r a t e d at the late follow-up, since patients w h o w e r e failures at the early follow-up are automatically excluded f r o m the late follow-up. As a result, a drug with p o o r efficacy at the early follow-up m a y a p p e a r better at the late follow-up. T o some extent this can be solved by analysing a c c u m u l a t e d efficacy, that is, the most negative o u t c o m e of both follow-ups [11]. Such an analysis also solves the problems o f patients w h o fail to r e p o r t for one o f the two follow-ups. T h e analysis o f bacteriological efficacy should be correlated to the one of clinical efficacy and vice versa.
Results
* Was the study sample representative for the population from which it was drawn? * Were risk factors identified and described? * Was clinical efficacy studied? * Was an intention-to-treat analysis performed? * Were data given for all patients randomized and reasons for exclusions after randomization described? * Were less than 5% of randomized patients lost to follow-up? * Were both early and late follow-ups of elimination of bacteriuria performed? * Was the early follow-up sufficiently late after the last dose to allow for at least 24 h of antibiotic-free urine? * Were reinfections and relapses differentiated by biotyping or serotyping in patients with recurrences caused by the original species? * Were bacteriological and clinical results correlated to each other and to susceptibilities to the antibiotics studied? Discussion and Conclusions
* If the null hypothesis was accepted, was the power of the study at least 80%? * Were differences between treatment efficacies, if demonstrated, likely to have been due to factors other than resistance of the causative organisms? * Can the results of the trial be extrapolated to a larger population?
expected to take it and r e s p o n d to it. A secondary aim is to detect biases of the investigators which are otherwise not obvious. T h e s e c o n d analysis o f clinical efficacy is p e r f o r m e d in
Conclusions
U T I is an extremely c o m m o n type of infection. Most cases are uncomplicated and easily treated with antibiotics. D u e to the high incidence o f UTI, even a relatively small miscalculation of the efficacy o f an antibiotic will affect a major g r o u p of patients if the drug b e c o m e s c o m m o n l y used for U T I treatment. Against this b a c k g r o u n d it seems p r u d e n t to d e m a n d a high quality of clinical trials in U T I patients. Studies including 30-40 patients in each group, finding no significant differences a n d concluding with a statement that the treatments w e r e "equally g o o d " no longer deserve to be published or p r e s e n t e d at scientific meetings. However, improved quality also means that U T I trials must in most cases include several centres. I n turn, it follows that the academic credits for the individual investigator b e c o m e minimal; often she o r he is r e d u c e d to a m e n t i o n in a f o o t n o t e of a study g r o u p publication. T h e only way to r e d u c e this p r o b l e m is to e n c o u r a g e subprojects which can be published independently. Such subprojects m a y be in microbiology, basic pathogenesis, pharmacokinetics or specialised safety analyses - all fields which are by no m e a n s p r e e m p t e d . T a b l e 3 is a suggestion for a list of questions which m a y be asked in each U T I study in o r d e r to ensure that basic quality requirements are fulfilled.
References
1. Norrby, R.: Quality of antibiotic clinical trials. J. Antimicrob. Chemother. 14 (1984) 205-208. 2. Fihn, S. D., Stature, W. E.: Interpretation and comparison of treatment studies for uncomplicated urinary tract infections in women. Rev. Infect. Dis. 7 (1985) 468--478. 3. Ronald, A. R.: Clinical trials of antimicrobial agents following licensure. J. Infect. Dis. 159 (1989) 3--6.
4. Working Party of the British Society for Antimicrobial Chemotherapy: The clinical evaluation of antibacterial drugs. J. Antimicrob. Chemother. 23 (Suppl. B) (1989) 1--42. 5. Finch, R. G.: The clinical evaluation of antibacterial drugs: Guidelines of the British Society for Antimicrobial Chemotherapy. Eur. J. Clin. Microbiol. Infect. Dis. 9 (1990) 542-547. 6. Gilbert, D. N., Beam, T. R., Kunin, C. M.: The implications for
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Europe of revised FDA guidelines for clinical trials of anti-infective agents. Eur. J. Clin. Microbiol. Infect. Dis. 9 (1990) 552-558. Lunde, L: Guidelines of the World Health Organization for clinical trials of antimicrobial agents. Enr. J. Clin. Microbiol. Infect. Dis. 9 (1990) 548-55t. Kass, E. H.: Asymptomatic infections in the urinary tract. Trans. Assoc. Am. Physicians 69 (1956) 56--63. Stamm, W. E., Counts, G. W., Running, K. IL, Fihn, S., Turek, M., Holmes, K. IL: Diagnosis of coliform infection in acutely dysuric women. N. Engl. J. Med. 307 (1982) 463--468. Urinary Tract Infection Study Group: Coordinated multicenter study of norfloxacin versus trimethoprim-sulfamethoxazole treatment of symptomatic urinary tract infections.J. Infect. Dis. 155 (1987) 170-177.
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11. Huitfeldt, B.: Statistical aspects of clinical trials of antibiotics in acute infections. Rev, Infect. Dis. 8 (Suppl. 3) (1986) $350-$357. 12. Byar, D. P., Sehoenfeld, D. A., Green, S. B., Amato, D. A., Davis, R., De Gruttola, V., Finkelstein, D. M., Gatsonis, C., Gelber, R. D., Lagakos, S., Letkopoulo, M., Tsiatis, A. A., Selen, M., Peto, J., Freedman, L S., Gall, M., Simon, R., Eilenberg, S. S., Collins, IL, Peto, IL, Peto, I?.: Design considerations for AIDS trials. N. Engl. J. Med. 323 (1990) 1343- 1348. 13. Norrby, S. R.: Short-term treatment of uncomplicated urinary tract infections in women. Rev. Infect. Dis. 12 (1990) 458-467. 14. Norrby, S. R.: Efficacy and safety of antibiotic treatment in relation to treatment time. Scan& J. Infect. Dis. (in press).
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