Observational studies belong to the analytic studies category, which is divided into experimental and nonexperimental design. In experimental design, the researchers control the intervention as part of the design. Experimental studies, and specifically randomized controlled trials, are considered the reference standard to assess the efficacy of therapeutic agents or prevention strategies for health conditions.1 The researcher controls the standardized setting and approach, and the subjects’ selection is based on strict and well-defined inclusion and exclusion criteria. The randomization should ensure a balance of known and unknown factors in the intervention and comparison groups. The randomized controlled trials aim to answer efficacy questions and to determine cause-effect relationships. Nevertheless, the well-controlled and manipulated environment can reduce the generalizability of the result to real-life scenarios. The high costs and the consequent short duration represent the main limitations of randomized controlled trials.1,2

In nonexperimental designs, the researcher observes associations between exposure or treatment and an event or effect (outcome). They are called observational studies because the investigator does not intervene on the study population and simply searches relationships, analyzing risk factors or medications and the disease.3 Observational designs are commonly related to epidemiology. They can measure the prevalence, incidence, proportional ratio, and accumulated new cases over time.2,4

In the eternal comparison between observational and randomized control trials, the need for good quality research unifies all researchers and clinicians involved in the field of physical and rehabilitation medicine (PRM).5

In PRM research, there could be more challenges than other fields as we are dealing with physical procedures or behaviors instead of drugs, so we will have to manage and assess complex interventions.6 We define complex interventions as those containing several interacting components, in which blinding is a challenge, and the interactions between different personalities can influence the outcome. In addition, measurements in PRM are complex and include patient-reported outcome measures or surrogate outcomes experienced by researchers.7

Different research questions require different study designs. Both experimental and nonexperimental designs are essential to increase knowledge and to improve management in the healthcare field. A basic knowledge of the differences between designs gives the researcher the power to understand and appraise the scientific papers and understand which design better answers a specific research question. When investigating the association between a risk factor or behavior and the development of disease or evaluating the effect of an already established method, an observational design could be the best way to answer the research question. Some examples of research questions effectively answered by observational design include: is there an association between bracing plus exercise therapy and the low back pain recurrence rate? Or, is there any difference in pulmonary function in patients with chronic obstructive pulmonary disease who underwent endurance training alone compared with endurance training associated with muscle strength? Or, are specific exercises associated with a lower rate of brace prescription in adolescents with idiopathic scoliosis during growth?

The advantages of observational designs include the lower costs and complexity in regulation and management in comparison with experimental studies. They allow the investigation of rare conditions. They have excellent generalizability because of the real-life environment, a usually larger sample size, and a longer follow-up than randomized controlled trials.8 Furthermore, observational designs offer the advantage to test multiple outcomes, and they provide more relevant and valuable information for everyday practice.9

Simplicity does not mean superficiality. Less complex does not mean less rigorous. Faster does not mean less time-consuming. Observational studies require an insightful and careful study plan after a deep research of all potential pitfalls and confounders necessary to be addressed before starting data analysis. We aim to give the readers an overview of the observational designs and guidance on how and when to use them and how to deal with the potential statistical traps in different observational designs.3

MEASURES OF ASSOCIATION IN PRM

In PRM, researchers could be interested in checking whether there is an association between a treatment and the natural history of a chronic or progressive condition. Comparative effectiveness research10 involves group comparisons of alternative interventions in which investigators are interested in finding out differences in the outcome for the currently applied approach compared with a new one.

Observational studies investigate an association between risk factors, treatment or procedure, and an outcome under real conditions in everyday practice settings.9 Two primary components of the association studies are the exposure and outcome. In epidemiology, exposure is a risk or prognostic factor, a diagnostic test, or a treatment, and the outcome is usually a disease, recovery from a condition or death. When aiming to check treatment effectiveness with an observational design, the exposure is treatment, and the outcome could be a binary variable (like success or failure), a multilevel ordered categorical variable (like pain score, disability scores from questionnaires), or a continuous measure of outcome (like range of movement, muscle strength measures, and many others).11

Risks, rates, prevalence, and odds are standard measures of the frequency of an outcome and comparing them between groups will yield relative frequency measures—that is, relative risks, rate ratios, prevalence ratios, and odds ratios. These describe the association between exposure and outcome and provide the basis for the study’s conclusions.12

NONEXPERIMENTAL DESIGNS Cross-Sectional—Snapshot Designs

Cross-sectional studies assess the population, checking the exposure and outcome status at a single time point (Fig. 1). With short time and limited funding, cross-sectional is the most accessible design: it is like a snapshot of the sample. The inclusion and exclusion criteria are based on the exposure status, regardless of the outcome of participants. Sample selection is crucial for cross-sectional studies, being the random selection method preferred to avoid selection bias.3 In epidemiology, this design is mainly used for prevalence estimations, and the results are commonly applied in public health policies. In PRM, it is used to describe the prevalence of a condition in the general population or one comorbidity in a population of subjects with a specific health condition/disability. A survey aimed to investigate the access to telecommunication technologies, and rehabilitation services of patients with multiple sclerosis and their willingness to use these technologies for rehabilitation is an example of a cross-sectional design study.13 Another example is a research to study dizziness frequency among stroke patients referred to rehabilitation in primary health care and its relationship with sex, age, activity, and self-rated health.14

FIGURE 1:

The three main study design used in observational studies: cohort, case control, and cross-sectional.

Generally, in cross-sectional studies, the investigators describe the sample, and the prevalence is presented in the overall sample and in subgroups by exposure or intervention with a 95% confidence interval.15 Among the most used statistical methods, there is logistic regression. In the last example, the binary outcome variable is presence or absence of dizziness, and the tested explanatory variables were age, sex, activity, and self-rated health. The logistic regression model investigates whether the explanatory variables are associated with higher odds of having dizziness in subjects with stroke.16

The main advantage of the cross-sectional design is the simplicity, but it is suitable for simple questions only. Be aware that this design cannot assess temporal relationships; therefore, a careful interpretation of results is requested.17 We can consider cross-sectional designs as preliminary studies to explore correlations and associations and guide future planning of more extensive longitudinal cohort studies.

Cohort Studies—Looking Forward Designs

Cohort studies provide the best level of evidence in nonexperimental design. They can be prospective or retrospective: in both cases, the direction of observation is from exposure to outcome. For the prospective follow-up, researchers will include the participants based on their exposure status and check who will develop the outcome.18 Time and data collection tools, such as clinical databases or registries, are needed (see the scheme provided in Fig. 1). In many progressive conditions in PRM, clinical monitoring and follow-up are needed to timely implement treatments and prevent the condition’s progression. For example, this happens in neurologic degenerative diseases, chronic low back pain, and degenerative orthopedic diseases. If all clinicians could systematically collect clinical measurements used in everyday practice in electronic clinical databases, we could share a large amount of data ready to be analyzed, thus offering better answers to improve PRM patient’s treatment. Other critical factors to have comparable data include standardized treatment strategies and outcome measures. In general, cohort studies require complex study planning and long follow-up and can be as expensive as experimental trials. However, they can suggest a strong causal relationship because of the temporal sequence between exposure and outcome. In PRM, they could improve research quality and, consequently, clinical guidelines and treatment recommendations.

In cohort studies, the subjects are observed longitudinally during the follow-up period. The investigator can compare the baseline with the end of the observation data or assess all the measures taken multiple times during follow-up. In the last case, we refer to panel data or hierarchical data: they offer the advantage to analyze differences between and within subjects. Panel data structure requires complex analysis, but when the aim is to investigate the effect of disease progression in a specific population, they offer more accurate and thorough analysis, thus producing more robust findings.19

Cohort studies allow examining multiple outcomes over time. Worth noting in this study design is the direction of time, going from the period without the condition toward a period that the participants could have experienced the outcome. An interesting example in PRM is a research aimed to determine the survival of patients for up to 10 yrs after a first-time stroke and to investigate whether rehabilitation within the first 3 mos reduced long-term mortality. The participants are exposed to rehabilitation after stroke with the expectation to reduce the risk of death. At the entry date, they must be free from the exposure: in the example, participants should have never been treated: in case of drug treatment, the researchers must check that the washout period passed.20

Cohort study can be retrospective, meaning that they start when participants already experienced the event of interest, and researchers investigate the exposure to evaluate when it occurred in the past.18,19 On the contrary, the cohort study is prospective when participants are recruited before experiencing the outcome and before exposure to intervention, like in a study to assess physical activity and sedentary behavior changes determined by cardiac rehabilitation for 6 wks.21

In cohort studies, the analysis typically compares the outcomes in exposed and nonexposed groups by calculating the risk or the incidence of the outcome in each group, and the ratio between exposed and nonexposed groups might be useful to highlight the differences. Analyses cannot occur until there have been enough events, so the prospective cohort design cannot be suitable for disease with long latency or rare outcome incidence.22

Case Controls—Looking Backward Designs

Case-control studies are traditionally considered retrospective based on the nature of design and execution. Patients who have developed an outcome are collected and compared with control subjects without the outcome. Researchers will compare the exposure to the risk factor(s) or intervention(s) between groups. Unlike the prospective cohort studies, the direction of enquiry on case-control study goes from the presence or absence of outcome to exposure, whereas in cohort studies, it goes from exposure to outcome.19

A case control is one of the most accessible designs. It is widely used but very frequently misunderstood (Fig. 1). According to Mayo and Goldberg,23 in PRM, case-control studies are frequently misclassified as cross-sectional. For example, to better understand possible functional limitations in medial epicondylitis, the researchers decided to call their study design a cross-sectional case-control study.24 When running a case-control study, time plays a pivotal role. The description of two groups of patients at a defined period ignores the dynamic nature of database collection. Therefore, the temporal relationship in cross-sectional design remains unclear and could affect the ability to answer a specific research question. In the previous example, it is possible to assess the impact of epicondylitis but not to compare whether medial is different from lateral epicondylitis. Because of the cross-sectional design, the researchers are unaware of the condition of nonparticipants. Other questions remaining unanswered are as follows: when in the course of the disease was the testing done? Are there any other factors influencing elbow and arm function? Is time from the onset of the pain influencing the outcome? A case-control study should always consider the time, to compare the cases and controls at baseline and at a prespecified end point. If the comparison is at a fixed time point, it is a cross-sectional design and the results are just assessing the impact of the disease in two groups, but no comparisons are allowed.

When designing a case-control study, it is essential to define cases and controls carefully. Cases would ideally include all the incident cases from the study period. When defining the controls, it is fundamental to sample a representative population exposed to the risk of the outcome, meaning that the control group shares the same inclusion and exclusion criteria. Another troublesome decision is the size of the control group: in the lucky situation that large sample size is possible, and the costs for obtaining information are not an issue, then the optimum ratio is 1:1. Investigators must be careful and aware that enlarging the control group is not enhancing the study validity, but it is just increasing the statistical power. A limited number of available cases or higher costs for obtaining information from control group will affect the study and make an unbalanced ratio the best strategy. Case-control studies have a high risk of bias, especially the recall bias, when subjects cannot remember whether they were exposed to the risk factor. The problem is more critical for the control than the case group.25 Despite some drawbacks, case-control studies are often more efficient than cohort studies, especially when dealing with rare outcomes or exposures that are difficult or costly to assess. Furthermore, they are usually cheaper and less time-consuming than cohort studies.26

Regarding the analysis, case-control studies usually infer whether the exposure is a risk factor for the outcome by comparing the frequency of exposure in cases and controls. Richardson et al.27 provided an interesting example: they investigated lifestyle risk factors for electrodiagnostically confirmed ulnar mononeuropathy at the elbow. They divided the recruited subjects into three groups: those diagnosed with neuropathy, those with a suspect of neuropathy, and healthy subjects (controls).27 They reported between-group differences in categorical and continuous variables using the χ2 test and analysis of variance. The relationships between continuous variables were determined with Pearson correlation coefficients, and logistic regression was performed using variables in univariate and multivariate models, including the demographic factors, smoke, and activity as potential predictors of ulnar mononeuropathy at the elbow.27 The model should take the pairing into account and should include the matching covariates.16

Specialized Study Designs

Beyond the most used designs, some special research methods help the researchers control confounders in specific situations: the interrupted time series, the self-controlled case series, and the active comparator new user designs.28–30

In the interrupted time series, the sequence of observation is interrupted by a sudden event or perturbations. An example could be the prevalence of acute low back pain before and after COVID-19 lockdown and consecutive mobility reduction in employees. Another example is the prescription of a new treatment procedure before and after the publication of guidelines recommending its use in a specific category of patients.28

The self-controlled case series involve cases before and after they experience the outcome. Each subject is its own control. A fundamental assumption of this design is that subsequent exposures should not be affected by previous events. Second event rates are constant within fixed time intervals, and the last event recurs independently.29

If these assumptions cannot be met, then the active comparator new users design can be considered. In this case, individuals with newly prescribed treatment A are compared with individuals with newly prescribed treatment B over some time. Notably, this design is not comparing initiators with nonusers or usual users to new users.30

CONFOUNDING

Quality of research affects both experimental and nonexperimental designs. Design analytical skills are essentials to handle bias and manage confounding in observational research planning, implementation, and reporting. Bias refers to any systematic error introduced during design conduct or analysis of any experimental or observational study, resulting in inaccurate estimates of treatment effects.

One of the most challenging bias to manage in observational studies is selection bias; it occurs when there is a systematic difference between the characteristics of participants selected for the study and those who are not. Consequently, the groups used for comparison differ in ways other than the intervention or exposure under investigation, and therefore, the study result is biased, limiting the conclusion drawn from the analysis.31,32

The randomization procedure will generate an equal chance for allocation between the groups under investigation in intervention trials. The goal is to create a balance between known and unknown factors during this process. There is no randomization process in observational design studies, which reduces the control for balancing risk factors or confounders. The missing of randomization procedures in observational designs reduces the control of unbalance between observed and unobserved confounders in the allocated groups. Confounding variables act to distort the treatment effect measures because they correlate with both treatment and outcome.2 An example of confounding is dietary habits, which confound the association between osteoporosis and vertebral fracture risk. Contrarily, the presence of spine deformities can be a consequence of osteoporosis but not a confounding. Restriction and stratification, regression adjustments, propensity scores matching, and instrumental variables are the most used methods to address confounding. A careful choice of the study design is an excellent strategy to control for confounders effectively.33

Restriction involves a careful selection of participants. It exposes to loss of some subjects but allows to control for confounding. Suppose we refer to the previous example of osteoporosis and vertebral fracture risk. In that case, if we suspect that the included population could be exposed to dietary deficiencies, exclusion of participants with lower body mass index or a diagnosis of anorexia could control this confounder.34

If the univariate model is possibly confounded, a good strategy consists of developing a multivariate model including all potential confounders. The potential confounders come from the scientific literature and clinical expertise and should be identified at the project stage.35

Another used to control confounders is ensuring their equal distribution among exposed and unexposed groups. This method is called matching. Different matching methods can apply; frequency matching is when we choose participants so that the distributions of the matched variables are the same. For example, if 45% of cases in the case group are men, then 45% of controls should be men. Individual matching consists of choosing a control with the same characteristics (e.g., living in the same neighborhood) for each case. The matching process increases the risk of making controls too similar to cases, affecting the results.26

In observational studies, there is the risk that the exposed and nonexposed compared groups had different baseline characteristics, thus introducing selection bias. Propensity scores allow estimating the probability of receiving a treatment based on baseline characteristics.36 Propensity scores check that the distribution of observed baseline covariates is the same between treated and untreated subjects. Therefore, if we individually match study subjects on their propensity score, we should find approximately similar distributions of covariates in treated and untreated groups. We could also adjust for the propensity score including it as a single confounder in the analysis, stratifying on it, or using it as a weight.

ANALYSIS IN OBSERVATIONAL DESIGN AND COMMON STATISTICAL TRAPS

During research planning, the first fundamental steps toward analysis are defining the type of data you have and the dependent and independent variable.29,30 In case of categorical variables, how many categories are there? Is there any pairing in the data? Regarding continuous data, checking the distribution of data and the missing data is an essential preliminary step before analysis planning. Table 1 is a helpful guide through the analysis suiting the available data.

TABLE 1 - Statistical analysis in observational studies Type of Bivariate Comparison No. Groups Independent Samples Paired Samples Parametric Nonparametric Parametric Nonparametric Categorical vs. categorical
Example treatment type vs. sex 2 — χ2 test
Fisher exact test — McNemar test Categorical vs. categorical
>2 levels
Example: disease severity  vs. religion >2 — χ2 test
Fisher exact test — — Categorical vs. quantitative
Example 2 treatment types  and mean SBP 2 T test Wilcoxon rank sum test Paired t test Wilcoxon signed-rank test Categorical vs. quantitative
Example 3 treatment types  and mean SBP >2 One-way ANOVA Kruskal-Wallis test Repeated-measure ANOVA Friedman test Quantitative vs. quantitative — Pearson correlation regression analysis Spearman rank correlation Generalized linear models — Time to event data 2 Log rank test
Cox hazard regression model

ANOVA, analysis of variance; SBP, systolic blood pressure.

When the plan is ready, an insightful check of potential sources of bias is strongly recommended. Another critical bias in observational design is immortal time bias.37 Immortal time is when participants of a cohort cannot experience the outcome during the follow-up. This bias usually happens when researchers assign participants to a treated or exposed group using information observed after the participant enters the study. In rehabilitation, this could happen when there is a variable time passing from prescription to the start of treatment. Bias is introduced if this “immortality period” is misclassified or excluded during analysis. We can run a statistical analysis that accounts for time-varying covariates with a multilevel logistic regression or survival models with time-varying covariates.35

Another trap is represented by multiple testing. It happens, for example, that we want to test two hypotheses: is temporomandibular joint impairment associated with scoliosis? Is flat foot associated with scoliosis? Remember that the more we test, the easier it is to get significant results. To control this, we could tweak the significance threshold with Bonferroni correction38 or tweak the significance level arbitrarily, for example, fixing the P value at 0.001 rather than 0.05. It is strongly recommended to decide the primary analysis at the research project study.39

Missing data management is another essential element to guarantee the best quality of an observational study.40,41 All the efforts should be addressed to minimize missing, report missing data, and define whether they are missing at random and will guide the choice on how to manage missing imputation.40,41

The statistical analysis plan is of paramount importance even in observational design studies. In the statistical analysis plan, a clear statement and definition of primary and secondary outcomes and the covariates of interest should be reported and decided a priori. The descriptive analysis to be carried out and the essential statistical methods, including addressing confounding, must be stated. The authors should declare how they will handle missing data and how the appropriateness of chosen statistical methods will be assessed. Finally, they should clearly state the primary analysis (linked to the primary outcome) and describe all planned secondary and sensitivity analyses.42

CONCLUSIONS

Observational studies have some disadvantages compared with experimental ones and the significant advantage of generalizability and representation of real-life situations. Data coming from observational studies are more challenging to manage and require more statistical knowledge and research skills. Nevertheless, because of the challenges7 and ethical issues in PRM,43 they are somehow more feasible and provide more clinically relevant findings. Standardized prospective data collection and registries could represent a decisive opportunity for future improvement of observational studies in PRM.44

REFERENCES 1. Benson K, Hartz AJ: A comparison of observational studies and randomized, controlled trials. N Engl J Med 2000;342:1878–86 2. Concato J, Shah N, Horwitz RI: Randomized, controlled trials, observational studies, and the hierarchy of research designs. N Engl J Med 2000;342:1887–92 3. Thiese MS: Observational and interventional study design types; an overview. Biochem Medica 2014;24:199–210 4. Black N: Why we need observational studies to evaluate the effectiveness of health care. BMJ 1996;312:1215–8 5. Horn SD, DeJong G, Ryser DK, et al.: Another look at observational studies in rehabilitation research: going beyond the holy grail of the randomized controlled trial. Arch Phys Med Rehabil 2005;86(12 suppl):8–15 6. Campbell NC, Murray E, Darbyshire J, et al.: Designing and evaluating complex interventions to improve health care. BMJ 2007;334:455–9 7. Fregni F, Imamura M, Chien HF, et al.: Challenges and recommendations for placebo controls in randomized trials in physical and rehabilitation medicine: a report of the international placebo symposium working group. Am J Phys Med Rehabil Assoc Acad Physiatr 2010;89:160–72 8. Horn SD, DeJong G, Deutscher D: Practice-based evidence research in rehabilitation: an alternative to randomized controlled trials and traditional observational studies. Arch Phys Med Rehabil 2012;93:S127–37 9. Horn SD, Gassaway J: Practice-based evidence study design for comparative effectiveness research. Med Care 2007;45(10 suppl 2):S50–7 10. Sox HC, Goodman SN: The methods of comparative effectiveness research. Annu Rev Public Health 2012;33:425–45 11. Anglemyer A, Horvath HT, Bero L: Healthcare outcomes assessed with observational study designs compared with those assessed in randomized trials. Cochrane Database Syst Rev 2014:MR000034 12. Tripepi G, Jager KJ, Dekker FW, et al.: Measures of effect: relative risks, odds ratios, risk difference, and ‘number needed to treat’. Kidney Int 2007;72:789 13. Remy C, Valet M, Stoquart G, et al.: Telecommunication and rehabilitation for patients with multiple sclerosis: access and willingness to use. A cross-sectional study. Eur J Phys Rehabil Med 2020;56:403–11 14. Hansson EE, Beckman A, Näslund A, et al.: Stroke and unsteadiness—a cross-sectional study from primary health care. NeuroRehabilitation 2014;34:221–6 15. Altman DG, Machin D, Bryant T, et al.: Statistics with confidence: confidence intervals and statistical guidelines [includes disk], 2nd ed. London, BMJ Books, 2011:240 16. Hosmer DW: Applied Logistic Regression, 2nd ed. New York, Wiley, c2000 17. Sedgwick P: Cross sectional studies: advantages and disadvantages. BMJ Online 2014;348:g2276 18. Barrett D, Noble H: What are cohort studies. Evid Based Nurs 2019;22:95 19. Song JW, Chung KC: Observational studies: cohort and case-control studies. Plast Reconstr Surg 2010;126:2234–42 20. Hou W-H, Ni C-H, Li C-Y, et al.: Stroke rehabilitation and risk of mortality: a population-based cohort study stratified by age and gender. J Stroke Cerebrovasc Dis Off J Natl Stroke Assoc 2015;24:1414–22 21. Freene N, McManus M, Mair T, et al.: Objectively measured changes in physical activity and sedentary behavior in cardiac rehabilitation: a prospective cohort study. J Cardiopulm Rehabil Prev 2018;38:E5–8 23. Mayo NE, Goldberg MS: When is a case-control study not a case-control study?J Rehabil Med 2009;41:209–16 24. Pienimäki TT, Siira PT, Vanharanta H: Chronic medial and lateral epicondylitis: a comparison of pain, disability, and function. Arch Phys Med Rehabil 2002;83:317–21 25. Ahrens W, Pigeot I: Handbook of Epidemiology. Berlin Heidelberg, Springer-Verlag, 2005 26. Schulz KF, Grimes DA: Case-control studies: research in reverse. The Lancet 2002;359:431–4 27. Richardson JK, Jamieson SC: Cigarette smoking and ulnar mononeuropathy at the elbow. Am J Phys Med Rehabil 2004;83:730–4 28. Bernal JL, Cummins S, Gasparrini A: Interrupted time series regression for the evaluation of public health interventions: a tutorial. Int J Epidemiol 2017;46:348–55 29. Petersen I, Douglas I, Whitaker H: Self controlled case series methods: an alternative to standard epidemiological study designs. BMJ 2016;354:i4515 30. Lund JL, Richardson DB, Stürmer T: The active comparator, new user study design in pharmacoepidemiology: historical foundations and contemporary application. Curr Epidemiol Rep 2015;2:221–8 31. Nunan D, Bankhead C, Aronson JK; Catalogue of Bias Collaboration: Selection bias. 2007. Available at: https://catalogofbias.org/biases/selection-bias/. Accessed May 6, 2021 32. Henderson M, Page L: Appraising the evidence: what is selection bias?Evid Based Ment Health 2007;10:67–8 33. McNamee R: Confounding and confounders. Occup Environ Med 2003;60:227–34 35. Harrell FE Jr.: Regression Modeling Strategies: With Applications to Linear Models, Logistic and Ordinal Regression, and Survival Analysis. Switzerland, Springer, 2015 36. Austin PC: An introduction to propensity score methods for reducing the effects of confounding in observational studies. Multivar Behav Res 2011;46:399–424 37. Lévesque LE, Hanley JA, Kezouh A, et al.: Problem of immortal time bias in cohort studies: example using statins for preventing progression of diabetes. BMJ 2010;340:b5087 38. Lee S, Lee DK: What is the proper way to apply the multiple comparison test?Korean J Anesthesiol 2018;71:353–60 39. Bender R, Lange S: Adjusting for multiple testing—when and how?J Clin Epidemiol aprile 2001;54:343–9 40. Altman DG, Bland JM: Missing data. BMJ 2007;334:424 41. Streiner D, Geddes J: Intention to treat analysis in clinical trials when there are missing data. Evid Based Ment Health 2001;4:70–1 42. Hiemstra B, Keus F, Wetterslev J, et al.: DEBATE-statistical analysis plans for observational studies. BMC Med Res Methodol 2019;19:233 43. Zaina F, Donzelli S, French MN, et al.: Ethics in rehabilitation: challenges and opportunities to promote research. Eur J Phys Rehabil Med 2016;52:267–70 44. Röder C, Staub L, Dietrich D, et al.: Benchmarking with Spine Tango: potentials and pitfalls. Eur Spine J 2009;18(Suppl3):305–11