Can trypanocidal therapy prevent chronic
Insights from a systematic review
Juan Carlos Villar
Universidad Autónoma de Bucaramanga,
Population Health Research Institute, McMaster University,
Whether trypanocidal therapy can prevent the development of full-blown chronic Chagas' cardiomyopathy (CCC) has attracted the attention of many researchers, clinicians and decision-makers over the years. Despite laudable contributions made particularly in the last decade, an active controversy remains as a result of inconclusive answers in this regard. This review attempts to discuss the extent to which the existing studies have provided information relevant to this extremely important question for the field. As an introduction, some general elements used to appraise the effects of health care interventions will be brought to attention, and discussed then in the context of CCC. A second section presents key data that have been generated so far. Finally, some potential ways to improve the body of knowledge in the field will be discussed.
I - Evaluating treatment effects:
What is particular for Chagas' disease?
a) Rationale for randomized controlled trials and meta-analyses
Quoting information versus grading scientific evidence
The principles and practice of evidence-based medicine have been increasingly adopted over the last decades. Recommendations that intend to guide busy clinicians in both appraising the literature and decision-making have been generated . Randomized controlled trials (RCTs) have become the standard tool to evaluate the effects of health care interventions . By allocating (experimental and control) interventions at random, and record afterwards a number of responses or clinical events among participants, RCTs are to measure the clinical efficacy of therapeutic or preventive intervention(s) being tested. Once the follow-up is completed, a trial will determine what the mean changes (of continuous responses) or incidences (of clinical events) in the study groups were. The effects are usually reported as absolute or relative, depending upon mean changes or incidences in the experimental group are subtracted from, or divided by, those in the control group. Investigators will come up with (mean differences or) risk differences in the first case, or (relative differences or) relative risks in the second. Whichever the measures are, they are yet to be considered "effect estimates", as they necessarily depart from "the true effect". Investigators are to make every effort to reduce the distance between the "truth" and the effect estimate produced by their trials. Consumers, on the other hand, must be aware of the determinants of that distance (bias). For clinicians, patients and policy-makers the availability of "scientific evidence" may be not enough. Rather than that, all parties involved in health care wish for valid (unbiased) evaluations to guide treatment recommendations. Thus, whenever available, scientific information should not be cited as "evidence" without being appraised and weighted on its validity.
The strength of the inferences we can make from trials varies,
as many aspects of their design and characteristics influence their validity.
Key points for validity in a trial are:
a) achieving a truly randomized allocation,
b) making sure the treatment being given/receiving remains concealed for all parties involved throughout the trial and,
c) recording outcomes whose measurement is considered reliable and potentially important to modify clinical practice.
Trials with predictable (i.e. not randomized) treatment allocation would be comparing participants with different disease severity, or perhaps other (even unknown) factors that may not make the study groups "comparable". Randomized assignment of treatment is intended to make the study groups "balanced" in all factors, not only those known (i.e. measured) by the investigators. By using this simple and powerful method, investigators can learn about the effects of the "only" factor participants are not "balanced": the experimental intervention. No balance between groups at baseline means that selected participants (by known or unknown factors) are receiving the intervention being tested. ("selection bias"). Trials making investigators or participants aware of what intervention is being given/received may judge/report some clinical findings directly or indirectly related with the study outcomes in a different way. This situation ("ascertainment bias") may lead to either overestimate or underestimate the effect of the experimental intervention. While RCTs recording "hard" outcomes (i.e. mortality or incidence of myocardial infarction) may be less affected by this bias, those evaluating "soft" outcomes (i.e. quality of life or "clinical changes") may be strongly affected by unmasked interventions, critically threatening their validity.
As ideal conditions are not met for all trials, their users are to be fully aware of the factors limiting or threatening their validity. Moreover, often interventions are evaluated for studies other tan RCTs, with a variety of designs and validity. That is why guidelines to "grade" treatment recommendations have been issued (Table 1). The grades for the more valid sources of information are higher. RCTs with "narrow confidence intervals" (see below) and meta-analyses of (homogeneous) RCTs are at the top of the list, whereas observational studies, case series and expert opinions are considered of less value for this purpose.
Table 1. Grades of recommendation and levels of evidence for therapy or prevention. Material adapted from the recommendations at the centre for evidence-based medicine in Oxford (courtesy Dr D.L. Sackett).
Even within the first level, trials (and meta-analyses including these studies) will have a variable degree of validity, which has lead to scales for quality assessment of trials . Quality assessment has become a formal requirement for meta-analyses of trials. Users, therefore, should not be satisfied by finding the terms "randomized", "placebo-controlled" and "double-blind" in the report, without checking how the features aforementioned were handled in the trial. There exist many instances by which randomization or other backbones of the trial design are subverted. For example, some treatment allocations would seem at random, but are in truth predictable. Examples would be to assign treatments based on the day (odds versus even, etc) patients are coming to the clinic, their chart numbers, etc. These sequences are regarded as pseudorandomized. Other important factors strongly influencing validity would be the number of events being compared (a function of the number of subjects randomized), the completeness of follow-up and compliance to the intervention, and the practice of "intention-to-treat" analysis. When data are analyzed that way, effect size is estimated on the number of subjects randomized, rather than on those completing the study follow-up. As not all "scientific evidence" can be considered equally valid, not all RCTs can per se provide "definitive" answers on treatment effects.
versus large numbers: importance of replicated observations
In other circumstances, the treatment effect may not be biased by a flawed design (systematic error), but lack statistical precision (as opposed to "random error"), represented by wide confidence intervals. When this happens, it is too uncertain where the "point" of the actual effect of the intervention is located. An "excess" of random error may even obscure whether the intervention causes benefit or harm. That is particularly true when wide confidence intervals do not allow investigators to detect a relatively small, yet clinically important effect of the experimental interventions (lack of statistical power). The extent of random error that can be allowed in trial to succeed in answering the research question is also dependent on the effect size of the intervention. Some interventions with large effect sizes may appear almost self-evident and not need trials to demonstrate their efficacy (i.e. penicillin for pneumonia or vitamin C for scurvy). However, this is unfortunately the exemption rather than the rule in health care. Instead, the interventions that "need a trial" for their effects to be determined would be those with mild or moderate effect size (typically 15-30% of risk reduction compared with placebo or standard care). Such interventions would precisely be the more vulnerable to systematic or random error. Therefore, the design of both unbiased and powered trials is needed to obtain valid answers to most questions on therapy or prevention .
The scenario faced for most RCTs implies that besides efforts in setting up all the design elements required for an unbiased study, investigators must manage to come up with relatively precise effect estimates for the expected effect size. On the basis of a properly designed trial, both statistical precision and balance of study groups at baseline will be directly proportional to the numbers of participants randomized. Small trials are indeed at higher risk of either finding untrue effect differences (type I error), or no effect when it does exist (type II error). Type I error would represent a "false-positive" result, whereas type II would be a "false-negative" study. Both errors can be reduced by replication of observations. Replication acts by increasing the ratio between the "signal" (the "average" effect) and the "noise"(the variability of the effect among participants). Variability of the effect is expected within any particular condition by different categories of participants. As a result, differences in the effect estimates can be anticipated across the spectrum of participants both within the trials (i.e. different results for diabetic and non-diabetic subsets of participants of the same trial) and between trials (different trial results for the same question being asked in two different countries). Immerse in that variability (the "noise"), each trial (or group of trials) is meant to yield a "general" effect estimate (the signal) for an "average participant" representing an "average case" of that condition. Even if narrow/strict inclusion criteria were set in a trial, such variability would yet exist, while potentially limiting comparability with similar trials. In addition to increasing the signal-to-noise ratio both within trials and between trials, replication is also a required condition for any theory in science. Even if a single, well-designed RCT is large enough, replication is desirable to achieve more precision, increase generalizability (external validity) and reduce the play of chance in generating extreme results.
Meta-analyses as replicates
of randomized trials
It may be opportune to bring here examples of type I and type II error, such as those put in evidence by two meta-analyses of RCTs by increasing the replication of the same observations. Let us take first the case of the trials testing magnesium sulfate in post myocardial infarction patients. A first set of 7 small trials including 1301 patients identified a favorable effect size (RRR=55%) . Later on, a large, simple RCT (ISIS-4) including more than 50.000 patients identified a neutral effect and unmasked an earlier type I error, largely because of the small number of events analyzed previously. A type II error can be exemplified by another meta-analyses of trials testing whether delivering thrombolytic therapy in bolus versus infusion had an effect on the incidence of intracraneal hemorrhage . To detect an adverse, infrequent effect reliably (<1% of patients treated) required a very large number of patients that a single trial (usually designed for estimating efficacy of therapeutic outcomes) was not powered to detect. Pooling the data on 103.972 patients included in 7 trials allowed investigators to identify a 25% increase in the risk of intracraneal hemorrhage that had been considered "neutral" in individual trials. Both examples show how data aggregation from trials increases the validity of our inferences on effects of interventions with moderate or small effect.
In practice, a single research group often does not have the resources of the access to study a large number of patients within a reasonable time window. Moreover, investigators from different groups or regions may come to similar ideas and want to conduct trials asking the same generic question. The dependency of validity on replication of observations, as well as the impracticability of conducting large RCTs at a single center is the common ground for creating research networks with capabilities to conduct large, multicentric RCTs. On the other hand, meta-analyses of trials help health care community by estimating more precise effect sizes (i.e. with narrower confidence intervals) of those from single RCTs, while evaluating how well results from a trial replicate themselves among others addressing the same question (heterogeneity analysis).
This section has stressed the importance of having not only "evidence", but seeking information provided by RCTs to learn about the effect of interventions whenever possible. Clinicians' decisions would not be well supported by relying only on "trials", but studies strictly adhering to the basic design principles of RCTs to avoid biases. Not only well-designed RCTs would be needed, but appropriately powered studies with small chance of Type I and Type II error. Finally, replication within large trials or between trials addressing the same question will further reduce the random error and estimate the effect sizes more precisely. Once these conditions have been met, trials would be " ready to use". At this point, further studies such as those dealing with cost-effectiveness, or the so-called "phase IV" trials (i.e. those dealing with efficacy and side effects one interventions are used in clinical practice) will help put together the evidence with different practice scenarios. Although few interventions in the medical practice have reached such an "ideal stage", that would be the point in which a clinician would have all "general" elements to make decisions on individual patients. Decisions are ultimately made at individual level, but clinicians do require general "signals" for guidance. The more valid and reliable the signals, the better their practice will more likely be.
b) Rationale for trials and meta-analyses
of trials in Chagas' disease
Role of patient-based research in Chagas' disease
The gap between what has been made by vector control programs in terms of stopping transmission of infection at southern cone countries and what medicine has to offer for preventing or reverting chronic Chagas' cardiomyopathy (CCC) among infected subjects is both unfortunate and inconvenient. Most of this contrast relies on the priorities and allocation of resources set by control organisms for targets whose complexity have been so far dramatically different. Given the available tools to work with, vector control has been considered easier to achieve and given more resources. The relatively easy victory of vector control in the short run may become difficult to sustain, unless continued surveillance (for areas already declared as "free of transmission") and/or renewed strategies are attempted (for Andean or Central American countries) (7;7). Some facts associated with the natural transmission of T. cruzi infection, as well as lessons from the re-emergence of other vector-borne diseases (malaria and, more recently, sleeping sickness) previously taken as controlled prompt to have multidimensional control strategies. Virtually all the burden of Chagas' disease comes from infected subjects turning into cases of CCC after its long latency period. Even in the unlikely event that transmission was completely and steadily stopped throughout the continent, decision-makers must bear in mind an anticipated burden for at least three decades, unless effective interventions to prevent or revert CCC are added to that picture . We all hope the success of vector control can prevail and extend, but also that patient-based research progressively emerges and take importance so the two approaches for control can be synergistic.
The desperate need for more patient-based research in Chagas' disease should not only be limited to therapy or prevention. As knowledge is mutually dependent and interconnected, the lack of good evidence in diagnosis or prognosis has an effect on producing evidence on interventions. As an example, the fact that confirming diagnosis of T. cruzi infection usually needs three different serologic techniques is very uncommon for infectious diseases. So does xenodiagnosis, yet the most effective method to isolate parasites from the host. Clinical diagnosis of CCC has not fully seen the incorporation of the diagnostic techniques introduced in cardiovascular medicine either. It is accepted that a 12-lead electrocardiogram (ECG) lacks sensitivity to detect other subclinical abnormalities seen in asymptomatic T. cruzi-positive serology carriers (T+). The lack of population-based data in other methods than ECG has contributed to the absence of diagnostic or prognostic criteria for early stages or subclinical infection. Studies focusing on therapy have extensively recognized the need of better diagnostic tools to assess the effect of interventions. Conversely, studies doing parasitologic diagnosis would come to more definitive conclusions if they collected reliable clinical information. Finally, the lack of a more precise clinical characterization (more visible perhaps for the "indeterminate" phase") has lessened the validity of many mechanistic or basic science studies that otherwise would have provided more credible inferences. In sum, the need for construct validation for many concepts in Chagas' disease seriously affects the generation of knowledge in therapy. As a result, the task of identifying useful interventions for CCC will not likely be the product of isolated efforts, or a single, brilliant study. On the contrary, all aspects of patient-based research will need a boost, the more, the better the results on therapy and, in general, on the health care for T. cruzi -infected subjects.
Challenges in trial design for Chagas' disease
Providing valid evidence on interventions to prevent CCC among asymptomatic positive serology carriers (T+) is therefore a rather challenging task. This explains why after almost 100 years of its description clinicians can not count on a trustworthy intervention yet, as opposed to most infectious or parasitic diseases. Even assuming that the agents being used were not the problem, all intrinsic features of Chagas' disease would bring enough difficulties to design such trials. Many logistic constraints towards these studies are the result of the many knowledge gaps in Chagas' disease mentioned above, added to its biologic features and socioeconomic context. Biologically, the particularly long latency period of incubation of CCC implies the need for an also unusually long follow-up for a trial. Likewise, that long-standing subclinical infection conveys a very low incidence of clinical events (i.e. 0.5-1% per year), which implies the need to recruit large numbers of subjects if a trial is to be powered enough. The anticipated effect size has also a place in this equation. Unlike acute T. cruzi infection, decades of use and cumulated experience have shown that the effect of TT is not as strong and noticeable. If this had been the case, we would have not needed RCTs to test these interventions. For instance, a trial following a cohort of 1000 asymptomatic T. cruzi chronically infected subjects would end up recording 50-100 events in 10 years to be compared between treatment arms, provided no dropouts occurred. Unless the effect size is too large (i.e. >80% of events occurring in participants assigned to placebo). Such number of events would leave a trial too exposed to the chance of type I or type II error. Furthermore, those results would still need replication for other trials. Within the usual effect size range, say a 25% relative risk reduction, a trial having a 10% cumulative incidence of events in 10 years of follow-up, with a power of 90% (the chance no to make a type II error) would need 5.526 participants randomized. For a trial within the same parameters, but with a 5% incidence of events, the need would be 11.572 subjects. Both the long-term follow-up and the low event rate would determine a need for a very large number of participants in that trial, making its logistic challenges proportional.
The impact of the constraints mentioned above adds to the limitations brought by the socio-economic context of Chagas' disease. The scenario has been traditionally one with high demands and few resources. That (demands/resources) ratio has been one major obstacle to embark in RCTs on prevention of CCC using trypanocidal therapy (TT). Even counting on sufficient resources to conduct such trials, investigators may find difficulties following long-term participants living in rural areas, for a variety of reasons. Generally speaking, the lack of social infrastructure in the countryside of many Latin American countries, even the social, economical or political stability in some regions would make difficult to conduct those trials. For participants living in the lower socio-economic strata, where participants in trials on Chagas' disease will more likely be, these problems may have higher impact. Most migrations and dropouts sue to socio-economic causes may be out of control for the investigators. Unfortunately, T. cruzi-infected urban immigrants are also living in the poorest conditions in those settings , making their acceptance to participate in trials perhas easier, but their adherence more difficult to maintain over time. Investigators, in such restricted context, have opted for studies with shorter follow-ups and/or smaller numbers of participants than needed to answer that question. That context will also make studies to record less expensive outcomes, sometimes at a cost of lacking precision and/or validity (i.e. ECG in lieu of other cardiac diagnostic tests). Finally, often the advantages of some new technological tools, usually more costly, cannot be applied to the field soon enough (i.e. quantitative assessment of parasitic load by PCR methods). Ironically, as a body of information many smaller studies leading to non-definitive conclusions become more costly than having fewer, but more extensive, powered and valid pieces of research.
Unfortunately for diseases such as CCC, a trial intended to answer a clinical question must record clinical outcomes. Clinical (especially "hard") outcomes are more credible events to support or change health care decisions. These outcomes are also more reliable sources of information on the disease being studied. For CCC, "soft" outcomes can even be misleading (for example, some ECG abnormalities can appear and disappear spontaneously over the years) or not proven as surrogates of clinical benefit (i.e. parasite-related outcomes). In our view, there has been a fundamental confusion in the fact that many studies looking at whether TT can improve the parasitic-related outcomes have been taken as studies looking at whether TT can cure or prevent CCC. Despite mechanistically reasonable theories about it, whether TT reduces parasitic load in chronic T. cruzi infection may not directly translate into clinical benefit. Readers may want to remember or review the case of the Cardiac Arrhythmia Suppression Trial (CAST), where class I antiarrhythmic drugs were associated with increase mortality of post-MI patients . In this trial, participants were allocated to study groups once reduction of extra-systole had been achieved with study drugs pre-randomization. Despite suppression of arrhythmia, an excess of mortality was observed in subjects receiving flecainide or encainide, and the trials had to be stopped earlier than anticipated. Trials, particularly large trials can be used as natural history studies, but they are also ways to prove our theories on mechanisms of disease. For Chagas' disease, whether reducing parasitic load with TT leads to better clinical outcome is to be proven by RCTs collecting both parasite-related and clinical outcomes in subjects treated. Despite costs, the sine qua non in this chain of causation is having the clinical outcomes recorded.
Can observational studies on treatment effects for
Chagas' disease be helpful?
It is because of all these elements that we need trials, and no other studies. For a case like this, observational studies are not likely to be of much help. Observational studies would be more acceptable if the effect were thought to be strong, the required follow-up were not that long, or the biases not as obvious . The more obvious confounding factor is the clinical indication of TT to patients, the reason determining the "exposure" to TT. In the absence of clear or widely accepted criteria to decide which T+ individual to treat, the way subjects are "exposed" to TT in observational studies will be driven by individual (i.e. not systematic) decisions. Probable factors influencing that decision such as clinical judgment, values, etc, are not measured, making differences between exposed and unexposed groups difficult to interpret. Moreover, the results across studies would not be comparable at all. The other particular source of bias comes from the long-term follow-ups. Many observational studies addressing treatment effects are retrospective cohort studies based on charts of treated and untreated patients. By the time these studies are set, the individuals with a "complete follow-up period" will largely be a selection of those with that potential. The longer the follow-up, the higher the chance to have selected populations in the studies. That selected population will be composed of treated and untreated individuals who have kept attending follow-up visits for several years. Those "exposed" will be more likely to have better response to therapy, better adherence and tolerance to the drug. In a population with a low-event rate being treated with interventions with comparatively high rates of side effects, it will result in an overestimation of the efficacy and underestimation of the side effects. Untreated subjects with no major complaints will be more prone to abandon a follow-up (unless being rewarded otherwise). On the other hand, those attending the clinic long-term are more likely to be patients with complaints or adverse outcomes. This progressive selection over time will tend to overestimate the effects. It should be emphasized here that the effect of the selection bias will also affect studies recording "hard" outcomes. Finally, the resulting overestimation of the effect will be further enhanced by having patients and physicians unmasked to the interventions they are being receiving/prescribing. Assuming that the effect of TT is not a big one, the threats to validity coming from observational studies in the context of prevention of CCC are probably too high for treatment recommendations to be merely based on this information.
Role of meta-analyses of trials
in Chagas' disease
At this stage of knowledge and probably in the near future, Meta-analyses of trials in Chagas' disease may play an important role. Although the validity of meta-analyses is largely dependent on the quality of the individual trials, aggregation of trials has the potential to answer some questions that individual studies can not. That can be particularly true for a scenario where trials are difficult to produce and are not often conclusive. A typical example in the current situation could be the aggregated information on clinical outcomes included in trials where the primary responses have been parasite-related outcomes. Besides, meta-analyses of small trials have been extremely useful as hypothesis-generators toward design of larger studies answering fundamental questions on therapy . Aspects of trial design such as what population to include/exclude, what event rate to expect, what responses to record can be enlightened by pooling data included in non-conclusive trials. In regard to the interventions, both the therapeutic and side effects can be more precisely estimated. All of these critical points toward the design of more definitive trials can be extremely well supported by meta-analyses.
Control of Chagas' disease will probably need that patient-based research emerges on the ground of sustained success of the vector control policies. However, for patient-based research to play its historical role, efforts must go beyond trials covering other aspects such as diagnosis, natural history and prognostic studies. Trial design towards identifying interventions that prevent the development of Chagas' chronic cardiomyopathy embraces many challenges as a result of the lack of context knowledge, its biological features and socio-economic context. In particular, the long latency period and small yearly event-rate of Chagas' cardiomyopathy determine the need for long-term follow-ups. Trials aimed to answer a question on prevention of clinical events need to record clinical events. All of this makes to produce such trials particularly challenging. Observational studies are not likely to be of benefit for this purpose, because the effect size is not thought to be large, the indication for treating patients not very clear, and the resulting selection bias proportional to the length of the follow-up. In this context, fewer, but larger, more valid studies may be a strategy both more cost-effective and high-impact for the health care of participants. Finally, at this stage of knowledge, meta-analyses of trials have an important role, particularly as hypothesis generators for trial design.
OF THE EXISTING DATA
A- Data on efficacy from clinical trials
We have conducted a systematic overview of randomized trials testing TT for T+ subjects . Briefly, we identified 5 trials involving 756 subjects randomized to different trypanocidal agents or placebo. The search involved screening tittles and/or abstracts from more than one thousand studies indexed in electronic databases (using English, Portuguese and Spanish terms). Two reviewers appraised independently pre-selected references in full to decide on inclusion. We extended the search by browsing the reference cited by papers and contacting content experts and pharmaceutical companies. The search has been updated up to May 2002. No new trials eligible for inclusion were identified since publication of that review.
The trials (listed in Table 2) were conducted in different countries and included both school children and adults. 145 subjects were randomized to Benznidazole (BZD), 27 to Nifurtimox (NFTMX), 207 to Allopurinol (ALLOP) and 217 to Itraconazole ITRA (participants initially allocated to placebo in Apts' trial, were after two months reassigned to either ALLO or ITRA). None of the trials collected information on clinical outcomes, other than incidence of ECG abnormalities. Instead, all trials collected information in parasite-related outcomes (T. cruzi serology status, antibody titers mean reduction and xenodiagnosis status). A summary of results of pooled data is shown in figure 1.
|Table 2. General characteristics of the included trials. * Primary and secondary, as stated by the authors in the report. REP: Design feature reported by authors. DESC: Methods used to ensure that feature described in the report. ¨ Participants initially in placebo were re-allocated to one of the active arms after two months of treatment. [+/-] description indicates pseudorandomised treatment allocation. NA: not available.|
|Figure 1. Overview of the effect estimates for data extracted on four outcomes pooled. Estimates are expressed as Odds Ratios (OR), using the method proposed by Yusuf and Peto, or standardised mean differences (SMD) and their 95% confidence intervals (95%CI), using the fixed models statistical approach. Antibodies mean changes are given in the units originally reported by authors. A negative difference means reduction of levels after treatment|
The results for xenodiagnosis were found to be heterogeneous across trials (p<0.001). Figures 2 displays the xenodiagnosis status after TT by different categories of participants. Two factors, treatment with nitrosamine derivatives (BZD an NFTMX) and positive xenodiagnosis at baseline were associated with heterogeneous results for this outcome.
|Figure 2. Heterogeneity analysis showing the effect estimates (as figure 2) for the rate of positive xenodiagnosis (xeno) after treatment, according to different categories of participants and/or trypanocide agents. The dashed vertical line follows the overall effect size estimate as shown in figure 2. * p< 0.001 for heterogeneity. NITRO-D: Nitroimidazolic derivatives. ALLOP: Allopurinol; BZD:Beznidazole; ITRA: Itraconazole NFTMX:Nifurtimox|
B- Data on efficacy
from observational studies
Clinical data from observational studies become relevant in the absence of this information in clinical trials. Using the same search strategy, we identified a number of observational studies evaluating the efficacy of TT in T. cruzi chronically infected subjects. Similar to trials, most observational studies evaluated parasite-related outcomes. However, some of them also recorded clinical outcomes, including mortality. As a work still in progress, we have included here data from some observational studies whenever they a) followed cohorts of both treated and untreated patients and b), recorded information on mortality. Table 3 shows the main characteristics of the studies included in this analysis. Study subjects enrolled by these studies were also from different age and clinical strata and conducted in different countries. Tables 4-6 summarize the data on mortality, incidence of heart failure and incidence of ECG changes respectively.
Table 3. General characteristics of five selected observational studies following cohorts of treated (with trypanocidal therapy) and untreated subjects with T. cruzi positive serology to (at least 2 positive serological reactions). All studies recorded information on mortality in the cohorts. * Children and adults. 1. Variable dosage of trypanocidal agents both within and across studies, according to the recommendations by the time the subjects were treated. In all studies the control group was composed of untreated individuals. 2. According to the report, as addressed in the general conclusion. 3. Rated from 1 (small) to 3 (large), according to the presence of 3 factors: a) the probability (intermediate or high) that study subjects represent the clinical setting where they were taken/sampled, b), the rate of dropouts during the follow-up and, c) the verification of balance between treated and untreated cohorts at baseline. 4. Rated from 0 (no handling) to 3 (use of several methods), towards reduction of confounding effects for the effect size: a) in the sampling or selection of participants, b) in the group assembling, c), in the analysis.
|Table 4. All-cause mortality rates reported in the observational studies listed in table 3. * According to whether p values is³0.05 when these proportions are compared using chi square tests.|
Table 5. Incidence of signs/symptoms of heart failure as reported by the observational studies listed in table 3. * According to whether p values is³ 0.05 when these proportions are compared using chi square tests. Not specified in the report (recorded in the study as part of general " clinical progress" of disease).
Table 6. Incidence of ECG changes as reported by the observational studies listed in table 3. * According to whether p values is ³ 0.05 when these proportions are compared using chi square tests. Not specified in the report (recorded in the study as part of general " clinical progress" of disease).
C- Data on side effects (all studies)
Overall, sde effects were reported in up to 20% of participants treated with BZD in Sosa-Estani's trial. No severe side effects (i.e. leading to drug discontinuation) were reported in this trial and 11% were considered moderate. In regard to trials testing drugs other than nitroimidazolic derivatives, side effects were reported in 10.3%, 9.7% and 6.7% of subjects assigned to ALLOP, ITRA y placebo respectively (p=0.412). Despite lower frequency of side effects, all clinical events rated as severe reactions (i.e. leading to hospitalization) reported in the trials were observed in subjects treated with these agents (1 case of severe Steven-Johnson syndrome). Blood markers evaluated in the trials showed no warning levels, or differences compared to placebo, except for transitory elevation of aminotransferases in 3 of 185 subjects treated with ITRA.
Side effects were also reported by most of the observational studies included. Viotti reported 20% of side effects in the cohort of seropositive subjects treated with BZD. Fabbro reported a 13.8% and 9.4% rate of dropouts during treatment with BZD and NFTMX respectively. Gallerano reported side effects in 30%, 43% and 17% of the 309, 130 and 95 subjects treated with ALLO, BZD and ALLO respectively. Finally, in the retrospective cohort study conducted by Lauiria-Pires reported that 35% of subjects treated with NFTMX dropped out at 30 days because of intolerance. For BZD-treated subjects the rate of dropouts for intolerance at 60 days was 30%.
This overview indicates the clear contrast remaining between the burden of CCC, and the extent of clinical research on the efficacy of TT as preventive intervention. Despite major public health importance, until now, all forms of TT for chronic asymptomatic T. cruzi infection have been tested in only 756 subjects included into five RCTs. However none of these trials were designed to evaluate clinical outcomes. As a body of evidence, the validity of the data can be questionable, as most included trials are small (<250 subjects randomized to active treatment) and failed to report key methodological issues. On top of the scarcity of the data, none of the outcomes shown in the figures were evaluated in all 756 subjects enrolled, making the information available even smaller. The amount and quality of the data cumulated in the form of RCTs points an urgent need to overcome the burden-to-research gap for this public health threat for Latin Americans, particularly those living in poverty. Despite the great success achieved by vector control programs, the body of information on treatment of subjects already infected gives Chagas' disease the category of neglected clinical entity in clinical research.
In the light of the existing data, the case of the efficacy of TT to prevent CCC is one of real clinical uncertainty. Treatment recommendations on the use of TT in T. cruzi-chronically infected subjects have been already issued . However, no experimental data are available to ascertain the effect of TT on the clinical outcome of these individuals. Data on clinical outcomes recorded in observational studies, on the other hand, mostly indicate a neutral effect. The way data were reported in those studies would make aggregation of data a mix of study-specific biases and study heterogeneity impracticable, unfortunately. Nonetheless, a qualitative or semi-quantitative approach can be yet possible, by taking the effect size reported, in the light of the study size, the extent of selection bias and handling of confounding (Table 3).
Data on clinical outcomes
Two RCTs reported the incidence of ECG abnormalities in participants with "indeterminate phase" at baseline. Acknowledging the remarkable effort of completion of a four-year follow-up of school children of suburban areas of Brazil and Argentina, only 7 events, 2 in the active group and 5 in controls were found. Such low number of events (in a surrogate outcome) does not allow any further speculation on the clinical effect of TT from trials. The information on the four-year incidence of events (roughly 5% in the control group) can be, however, key for design of future trials.
Four of five observational studies comparing all-cause mortality in treated versus untreated subjects reported neutral effect. That was also the case for the incidence of heart failure and ECG changes. The results of the only "positive" study could not be replicated in any of these outcomes. Interestingly, that "positive" study showed very strong effects of TT on mortality (unadjusted RRR 76%, 95%CI= 47%, 89%). Being the largest study (n=1203) such large effect size would drive aggregated results toward positive results. However, both the second largest study (Cattlioti, n=775) and, more important, the study with higher quality standards (Lauria-Pires) yielded neutral effects. This raises the possibility of type I error as explanation for the effect size of the study lead by Gallerano. This may also be the result of the biases in observational studies discussed above. In many other contexts RCTs and observational studies addressing the same question have estimated discordant (sometimes largely discordant) effect sizes . On the other hand, the neutral result in most observational studies is probably in favor of the hypothesis that clinical effect of TT may be small to moderate. In fact, given the probability of that effect size, these studies may have been clearly underpowered. In sum, we have not been provided with any experimental data on clinical outcomes, and those from observational studies cannot be considered indicative of any particular direction to follow for that clinical question.
Some particular points in the design or report of the observational studies included deserve emphasis here. First, the overall positive effect reported by Viotti was due to evaluating the effect of BZD in terms of "all clinical changes" recorded in the subset of participants younger than 50. This approach gives similar value to the appearance of heart failure symptoms (from group II to group III) and the incidence of ECG or radiologic changes (from group I to II), which may be interpreted as outcome measurement bias. Fabbro presented the information in similar fashion, but reported no statistically significant differences. Second, the strategy used by Lauria-Pires's study included a random selection of subjects to perform T. cruzi serology, then a matched to those who had not been treated. This last group was in turn matched to seronegative subjects from the same sampling frame selected at random. It has been argued that sampling method used by this study lead investigators to select participants who were already "treatment failures", explaining the lack of differences between treated and untreated subjects . However, evidence from both RCTs and observational studies shows that that 90-100% of T. cruzi chronically infected adults is expected to yield positive reactions to conventional serology after being treated with TT. The selection bias caused by this sampling strategy would be therefore very small, if any. Instead, this study took random samples from its universe to identify positive serology carriers and then matched those who had been treated with untreated, infected "controls" by age and gender (i.e. nested case-control design). All of these features reduce the selection bias and the confounding, adding validity to that study.
Data on parasite-related outcomes
The effect of TT, in particular Nitroimidazolic derivatives, on parasite-related outcomes was shown to be both large and consistent across trials, populations and outcomes measured. The strongest evidence was found for both children and adults treated with BZD. This agent reduced by 90% the rate of positive xenodiagnosis and positive serology, using the AT ELISA technique. The effect of NFTMX in adults was similar to that of BZD on xenodiagnosis, the outcome where this comparison was possible. Other drugs (ALLOP and ITRA) had significantly smaller effects on xenodiagnosis. The effects on serology depended upon the technique used. Unlike AT ELISA, data on conventional serology were rather neutral. None of the adults treated in Coura's trial with either BZD or NFTMX changed their (conventional) serology status after treatment. Likewise, 39 of 44 Children treated with BZD and 42 of 44 treated with placebo had positive serology after 4 years of follow-up (p=0.433, Fisher's exact test).
Data on xenodiagnosis notoriously differed if expressed as relative or absolute proportion of positive tests. Despite a large relative effect size (i.e. RRR of 80-90%), the rates of positive tests at baseline (or after follow-up of placebo-treated subjects group) demonstrated poor sensitivity. Taking all data, only 70 of 296 (23.6%) of xenodiagnosis performed in seropositive participants assigned to placebo were positive. These very low rates make its use unreliable, even though substantial relative effects were attained. In addition to its low diagnostic accuracy, the test can become very uncomfortable for patients, who are directly exposed to live reduvidae nymphs for one or two days. Nonetheless, as shown in the trials analyzed, xenodiagnosis is still the most widely used tool to confirm parasitologic diagnosis. That prompts the need for more sensible and performable techniques for both parasitologic diagnosis and evaluation of trypanocide effects.
That may be the case of PCR. Although not reported in the trials mentioned, the recent appearance of PCR techniques in Chagas' disease may be promising to assess trypanocidal effects during the follow-up of participants in trials. PCR is much more sensible than xenodiagnosis, while keeping its good specificity . Conventional serology, on the other hand, is the most widely accepted standard for diagnostic purposes (if confirmed by at least two different techniques), but its value as surrogate for parasite clearance, is still to be proven. In these data, while Coura's reported a highly significant (relative) reduction of the rate of positive xenodiagnosis in participants receiving NFTMX or BZD, the author reported no changes in the conventional serological status in any study participant, regardless treatment allocation. A recent study has reported a 3-year follow-up of parasite-related outcomes in Children receiving TT. A persistently positive reaction to conventional serology was observed throughout the follow-up, whereas PCR become negative within the first 6 months and remain negative throughout the follow-up . Other serologic techniques, such as AT ELISA, may be promising ways to evaluate trypanocidal activity in treated patients as observed in these trials. Both Andrade and Sosa-Estani trials reported high rates of seroconversion and highly significant differences between BZD and placebo using that technique. The lack of a gold standard to assess trypanocidal activity urges to evaluate this outcome by combining both "conventional" and "diagnostic" techniques in future trials.
It has been suggested that a negative conventional serology after treatment is a reliable criterion of "parasitologic cure" . According to that opinion, the data from Coura's and Sosa-Estani would be suggesting that TT has a very low absolute efficacy to suppress trypanocidal activity (less than 10% in Children and perhaps no activity in adults). This hypothesis is yet to be proven in clinical trials testing TT and recording data in both conventional and novel parasitologic techniques. But even more important for decision-making on infected subjects, the prognostic meaning of different levels of parasitic load is to be proven by RCTs that record simultaneously parasite-related and clinical outcomes.
Lessons from other experiences to
be learned for Chagas' disease
There is no reason to believe that clinical research on treatments to prevent CCC needs a different approach to what has been done in other fields. On the basis of political willingness and appropriate resource allocation, other diseases, even those particularly challenging have been illuminated by biomedical research, and a great impact attained. Let us take the case of patient-based research on HIV infection. For a problem described only 20 years ago, clinicians can count already on reliable diagnostic tools, assessment of viral load to both guide therapy and make prognosis as well as interventions that are highly effective to stop progress or avoid maternal transmission . From being a lethal, hopeless situation for those infected in the 80s, HIV infection has turned to be a chronic, long-latency health concern in such a small time frame, despite its big complexity. Moreover, as opposed to what we see in Chagas' disease, patient-based research in HIV is taking the lead over prevention of infection. Although research in treatment for Chagas' disease faces many and serious challenges, no comprehensive strategy can be started without sufficient resources and sustained political interest from decision-makers at governments, public health organisms, granting agencies and some other organizations involved. Provided these resources are put in place, patient-based research (chiefly that leading to treatment of infected subjects) would probably have a great potential to provide, similar to what academia has achieved for other diseases.
Even more abundant and valid data than what are available for Chagas' disease have been considered either inconclusive or unacceptable as source to guide clinical recommendations in other fields. For example, the data from trials on mammography for preventing breast cancer have lead to different interpretations and a hot debate. Some has suggested to producing new data, setting longer follow-up periods and involving more participants as formula to overcome the uncertainty and settle that discussion . In the case of statins for vascular dementia, observational data suggesting a 30% reduction have not been considered a trustable enough proof to support recommendations . In general, the principles of evidence-based treatment recommendations should apply universally, no matter what the disease and its socio-economic context are.
Conclusion and final remarks
The present overview demonstrates a critical absence of sufficiently reliable and conclusive data to guide decisions on the use of trypanocidal therapy in subjects chronically infected by T. cruzi. In spite of a promising body of information, it is by no means a proof to either support or remove the use of this intervention to prevent cases of chronic Chagas' cardiomyopathy. All parties involved, governments, academic community, control organisms, granting agencies, charitable organizations and patient advocates should concentrate in, and work together for, closing the huge gap between the burden of Chagas' disease and what is to be offered to infected subjects. The interpretation of this sparse information though, can be very useful as guidance for the design of large, albeit simple and cost-efficient trials with capabilities to answer questions on prevention in a more conclusive fashion. As opposed to keep producing small trials looking at parasite-related outcomes, observational studies, or trying to interpret this tiny information, Latin American health care academic community should realize the need for large trials recording clinical outcomes and embark in unprecedented efforts to take that challenge. Taking that more cost-efficient path in the long run, researchers will be able to provide an answer to that fundamental question more reliably and move forward towards other secondary or future questions.
Considering the developing stage of patient-based research Chagas' disease is still in, the effort needed is both large and multidimensional. First, we need a huge research synthesis. There are so many insights and progress to be made by pooling information on aspects of Chagas' disease other than therapy. This review on therapy, for example, shows how the field has been provided with many small to mid size clinical studies looking at diagnostic and natural history issues. Putting these studies together coherently would offer really valuable information. Perhaps task forces should be created to lead these synthesis exercises and to make sure these studies result in recommendations (or directions at least) for clinicians. Second, we need more collaboration among academic community members. In the face of such a high demands-to-resources ratio, there is no much room for embarking in isolate efforts within the field. On the contrary, exemplary collaborative studies on Chagas' disease should be emulated by researchers from as many countries and areas of expertise as possible. More collaboration will produce greater, more meaningful and valid studies to tackle those critical questions still waiting for answers. Third, we need more and better drugs. The lead that public health authorities have already taken in that regard is more than welcome. It should be emphasized that interventions with as much as 20-30% of dropouts because of side effects are not likely to be applied as general measure of public health, in particular in the context of low event-rate, long-latency diseases such as Chagas'. Research aimed to identify new targets for drug design, or testing trypanocidal effects of drugs initially designed with other purposes should be stimulated so that trials in the field can succeed. Fourth, we need trials. For the trials we need, such task is particularly challenging, even risky, given the current stage of context knowledge, political willingness, resources offered and interventions available to investigators. However, it is the responsibility of Latin American academic community to accept it and work these obstacles out. More research synthesis, collaborative efforts and cost-effective study designs may greatly contribute to fueling this purpose. The continent cannot afford to keep having a neglected disease causing so much social burden anymore. By using feasible strategies in different ways, we should be able to produce the information needed to make a significant contribution to reduce the burden of disease. Meanwhile, vector control should obviously be maintained in the southern countries and extended to the Andean and Central American regions.
Finally, as for recommendations and choices on therapy based on the existing information, our attitude should not differ from that in other diseases facing similar situations in history. Sometimes, when information is either no available or convincing, the choice to make both ethically and scientifically is to enroll a patient in a trial. Think of asymptomatic HIV+ subjects coming to a clinic 10 years ago. Clinical trials have made the difference for the care of these subjects and can obviously make it for Chagas' disease. In the light of the clinical uncertainty we are facing for this question, our recommendation cannot be other but to conduct the trials we need.
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