Levels of evidence are defined by the study design and execution, and designs have been variously graded by their potential to eliminate bias [10, 11]. A hierarchy of study designs was first proposed by Campbell and Stanley [10]. The concept of evidence levels has been widely promoted since then to grade recommendations for clinical practice. The dogma of an RCT and RCT-based meta-analyses having superior evidence over an observational study has long been held as gospel despite numerous appeals to reconsider and to adapt the evidence levels [11–16]. The reasons for this may be that the only available evidence pyramids focuses on efficacy studies, which allow for an accurate assessment of cause and effect. The terminology “observational” connotes that the data were collected without interference, so the decision to assign patients to an exposure is not random and may be self-determined by confounding variables that are highly correlated with the outcome. As a result, an observed significant difference in outcomes may not necessarily be attributable to the choice of treatment alone but to the confounding variable (or to some combination). Thus, according to the current evidence-based medicine practice, a small sample-sized RCT would bring undoubtful superior evidence than a large observational study. RCT study design has a high acceptance in all clinical disciplines despite a long list of its limitations such as ethical considerations, organizational burden, complexity of random allocation, complexity of blinding, time and personal resources consumption, compromised integrity of the clinical context, difficulty in studying rare events and outcomes in distant future, limitations in evaluation of population-based interventions [11], sample size limitation for definitive results [17], patient refusal of participation, narrowing of the studied population, and limited external validity [18], as well as financial efforts. This is also despite the fact that so many efforts are required to answer only one main posed hypothesis in an RCT and the fact that the number of non-randomizable clinical questions is by far much higher than the number of randomizable ones.

In orthopedic surgery and traumatology, among other medical disciplines, it is often difficult to provide an ethically justifiable patient randomization for differing and often insufficiently studied treatment methods. In medical disciplines other than surgical ones, like in conservative treatments or in pharmacology, the effect of a treatment is often assessed in comparison to a placebo. In surgical disciplines and particularly in orthopedic implantology, placebo comparisons are difficult to imagine. This is a nonnegligible and important organizational restriction of a randomized controlled study design. There are particular questions in implantology which may justify an RCT; however, the method of choice for implant comparisons is a registry with sufficient participation to ensure high external validity, i.e., generalizability of results to the routine clinical settings [19]. Particularly when introducing new implants and aiming at postmarket surveillance, an observational approach allowing for benchmarking of new and older implants appears to be the most reasonable one [19].

Moreover, one should be aware that a large observational cohort and an RCT are per se designed to answer different questions, and their different goals and setups result in their different characteristics (Table 54.1). Importantly, while an RCT answers the question “can it work?” an observational study addresses the question “does it work?” [20] In a large dataset, one could add “in whom does it work best?” as one of the key questions that the large observational comparisons can answer, since they include better and poorer indications for a certain therapy, as it is mostly the case when an innovation is adopted by the larger medical community. Table 54.1 summarizes characteristics of an RCT versus registry.

On the other hand, strong evidence exists on the similarity of the results in RCTs and in observational studies. Benson and Hartz reviewed RCTs and observational studies between 1985 and 1998 and found that in a vast majority of therapeutic comparisons, the estimates of the treatment effects from observational studies and randomized controlled trials were similar [13]. In the same time, Concato et al. reviewed literature between 1991 and 1995 and concluded that the results of well-designed observational studies with either a cohort or a case-control design do not systematically overestimate the magnitude of the effects of treatment as compared with those in randomized controlled trials on the same topic, as it is anticipated [12]. In orthopedics, Bhandari et al. have shown that, when adjusted for important risk factors, the results of observational studies (n = 13) on revision and mortality rates after internal fixation of femoral neck fracture were similar to those in RCTs (n = 14) [21]. Equality of the results in an RCT and in a cohort study was shown also in spinal surgery based on the results from SWISSspine registry [22] and the Spine Tango results of a single center [23].

The proponents of an observational study design are often opponents of an experimental approach and vice versa. In 1996, Black wrote that there is no perfect study design and that “the false conflict between those who advocate randomized trials in all situations and those who believe observational data provides sufficient evidence needs to be replaced with mutual recognition of the complementary roles of the two approaches” [24]. Spinal surgery is one of the youngest and, in the same time, one of the fastest growing clinical disciplines with high and further growing epidemiological and financial impacts on society. The evidence demand in spinal surgery is therefore high, and there is a compelling need for quality assurance, outcome research, and postmarket surveillance of spinal implants.