"You can't always get what you want": from doctrine to practicability of study designs for clinical investigation in endometriosis

The scenario emerging from this survey investigation conducted on a study population of Italian women with endometriosis, poses fundamental questions to clinical investigators in this specific area of research. In fact, only a small minority of patients would accept enrollment in a RCT on the treatment of pelvic pain. If this situation is not limited to our referral centre, generalizability of results of trials might be prevented even when planning multicentre studies in order to overcome difficulties in recruitment. In fact, the external validity of trials conducted on extremely selected study groups would be low, limiting the possibility of extrapolating findings to a broader, heterogeneous population.

Moreover, a comparison between medical and surgical therapy would be practically unfeasible, thus confirming that patients are not prone to be casually allocated to very different options [25‐30]. This could potentially further distort the evidence, as only selected RCTs could be conducted (i.e., between two different medical treatments, but not between a medical and a surgical treatment), thus preventing complete assessment of all available interventions, as previously suggested [31].

Women appear nowadays much better informed than in the past, and wish to discuss treatment alternatives and to choose the option that best fits with their personal needs and expectations. In a sense, randomization impedes this tailored choice. This is confirmed by the fact that the most frequently selected option on both questionnaires was the patient preference trial. In other words, only some patients seem to be still willing to participate in clinical research and, in most cases, at their conditions, not at investigators’ conditions. In particular, 95 % of participants in our survey would decline blinding.

A potential drawback of our study lies in the characteristics of our participants, who are self-referred from the entire country, and sometimes have already undergone unsuccessful medical treatments or surgical procedures. Possibly, they might have a higher than usual level of knowledge on their disease, and of information on centers of expertise. It could be argued that this type of survey should be conducted only on women who have never been previously treated medically or surgically. Yet, this collides with the possibility of obtaining a definite diagnosis in most patients. Moreover, a laparoscopy performed with diagnostic purposes, eventually means treating that patient surgically in case endometriosis is found, as it would be unethical to visually confirm endometriosis without excising the lesions. In addition, the pattern of answers was not different in the 301 women who had already undergone a surgical procedure and the 199 who were never operated, thus questioning the impact of previous treatment on the study outcome. Finally, a misdiagnosis bias in the latter group appears highly unlikely, as the diagnosis of endometriosis was based on robust clinical, ultrasonographic, and histological evidence [32]. As study participants were all assisted by the National Health Service, a potentially spurious association between socioeconomic status and propensity toward participation in clinical research can be safely ruled out. More in general, clinical investigation is usually conducted in tertiary care centers thus this appear to be the type of population that would be considered for recruitment in a RCT anyway.

The groups of women that would accept or decline randomization in a trial on medical treatment did not differ significantly. However, our study was not originally powered to investigate the distribution of baseline characteristics between the two subgroups of women. Indeed, the number of participants was large and women were recruited consecutively, thus limiting the possibility of selection bias. Patients were carefully instructed about the different types of experimentation, on the objective of the present survey, and on the hypothetical nature of our inquiry, which would not have implied future obligations. They were allowed to ask questions and obtain clarifications by dedicated medical personnel. In addition, the compilation of the two questionnaires was very simple and could be performed rapidly. This helped avoiding refusals to participate in the survey.

Women could not select more than one option. This can be considered as another weakness of our survey and may explain why the patient preference trial was the most popular choice. Allowing women to choose more than one study design option, and structuring questions in a less “leading” format, would have probably helped clarifying whether randomization was absolutely unacceptable or would be a possibility.

Several investigators recently focused on the growing barriers to the conduct of RCTs, describing in details the types of impediments and suggesting different modalities to overcome unnecessary obstacles [5‐8]. On the other hand, estimates of effect size in large observational studies may be precise, but remain substantially weakened by bias and confounding that only random allocation can control [8]. Indeed, the problem here is different: in spite of all shareable methodological considerations, RCTs in the endometriosis area appear increasingly difficult to conduct, at least in Italy, specifically because the vast majority of patients would decline random allocation.

The adoption of the partially randomized patient preference trial design, in which participants who do not accept randomization are allowed to chose their preferred intervention [33, 34] or of the response-adaptive randomization trial design, in which the ratio of participants assigned to each arm are actively adjusted in favor of the better performing intervention based on already available data of patients previously recruited [35], does not seem to overcome the basic issue of unwillingness to accept randomization. In any case, the resulting group of women allocated by chance would be too small to be representative of the population of women with endometriosis. Moreover, the administrative burden and the costs would be substantially the same as for the standard two-arm clinical trial design.

To complete their studies, several investigators conducted part of the trial based on random allocation of treatments, and part based on patient preference [25, 26, 29, 36]. Interestingly, more patients generally chose the patient preference option than the random allocation one. Moreover, both the estimates of effect size and its precision were substantially similar in the two study populations [25, 26, 29, 36]. Additionally, it has been reported that the results of well-designed observational studies are generally similar to those of formal RCTs [37, 38]. Therefore, when preferences based on informed expectations exist, observational methods may be an alternative to RCTs [39, 40].

When the objective is the comparison of already approved treatments for endometriosis (i.e., phase IV studies, thus excluding truly novel, experimental interventions), observational studies are easier and less costly to conduct than RCTs, can be carried out in “real world” patient populations, and can be prolonged for longer periods on a large number of participants, thus providing robust evidence on safety of interventions [2]. As treatments are not allocated randomly, multivariable statistical models must be adopted to control for potential bias and confounding factors. The physician’s selection of patients who should receive the treatment constitutes one of the main confounders in observational studies. Therefore, it is important to try to limit this bias. Considering the two hypothetical comparisons of our survey, two different study designs could be adopted when RCTs appear unfeasible.

When large differences exist in the type of treatments to be compared and in associated morbidity (in our survey, medical versus surgical treatment), the patient preference trial might constitute a practical alternative. Differently from an observational study comparing two case series, where clinicians allocate treatments, in the patient preference, parallel cohort trial, treatment allocation is by patient choice. Whereas clinicians may be prone to recruit different types of women to the two study arms, allocation by the patients themselves should improve external validity. It has been suggested that preference-based treatment allocation may optimize cost-effectiveness of intervention [41], also because this research environment may be more similar to practical life conditions [33]. In case of functional outcomes, a comparison between two groups of participants who have chosen their treatment emphasizes patient satisfaction, thus representing the maximum possible effect size of the intervention [42]. However, a major selection bias is introduced in a study based completely on patient preference, thus limiting the interpretation of the findings. Moreover, the effect observed under these conditions can be referred exclusively to patients who specifically choose that treatment [43].

When two similar treatments are being compared (e.g., a new versus an old progestin, or a progestin versus a combined oral contraceptive), the patient-preference trial design does not seem suitable, as women may not be able to clearly express a definite preference. In these cases, the before and after study (or pre-post study), a quasi-experimental design, may be an option [44]. The before and after study is usually adopted at a system level (clinics, hospitals) to compare outcomes before and after an intervention is implemented [45]. A before and after study design could be used also to evaluate treatments, provided some conditions are satisfied. In this case all new cases of patients with symptomatic endometriosis would receive the same, standard medical therapy for a pre-planned period of time, at the end of which all new cases with the same clinical characteristics would receive the new medical treatment for the same period of time. The study gauges the difference in the effect of the new drug compared with that of the standard one.

In order to infer that a variation in outcomes is the consequence of the implementation of the new treatment, the characteristics of the participants in the “before group” must be similar to those in the “after group”, otherwise such inference would be seriously flawed. In order to avoid a selection bias, all eligible patients observed before the introduction of the new intervention must be included in the “before group”, the new treatment must be implemented at a precise time point, and all eligible patients observed after that cut-off time must use only the new treatment and be included in the “after group”. Any admixture of different treatments during the study period would invalidate the findings. There should also be no evidence of a prevailing temporal trend. Still, without a control group of patients in whom no variation in the intervention has been implemented, it may reveal difficult to ascribe differences in outcomes to the change of medical treatment. Moreover, only random allocation of treatments allows genuine comparability of the study groups. In a before and after study, even a modification in referral pattern during the study period may result in the creation of populations that may differ for several characteristics, such as severity of symptoms or type of lesions. Since it is unlikely to be able tocontrol for all known and unknown characteristics that may influence the outcome, it may not be possible to exclude that any observed between-group difference in a before and after study is due to confounding [45].