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A nonmathematical illustration of competing risk analysis A B Figure 1 Cumulative incidence of depression derived from the Kaplan -Meier method (panel A) and the cumulative incidence function (panel B) Subdistribution hazard model As expected with a higher rate of depression for females associated with a reduced rate of death, we observe more females than males diagnosed with depression at any point during the study. Being female increases the probability of depression, resulting in an 84% higher relative incidence of clinically relevant depressive symptoms for females than for males (adjusted HRsd 1.842, 95% CI 1.430–2.370), whereas it decreases the probability of dying before the onset of depression. The relative incid ence of death was more than 35% lower for females than for males (adjusted HRsd 0.639, 95% CI 0.547–0.746). Survival probabilities can be calculated for each individual by combining the subdistribution hazard ratios with their baseline hazard, just like on e would do with the hazard ratios derived from a Cox model in a situation in which no competing risks are present. In conclusion, sex has a more pronounced effect on the incidence of depression than on the cause-specific hazard of depression, as evidenced by the finding that the HRsd (1.842) was larger than the HRcs (1.537). The apparent increase in the absolute risk of depression for females might be explained via the effect sex has on death before the onset of depression. Discussion In epidemiologic research, competing risks are generally not considered in the analysis of survival data. In the presence of competing risks, cumulative incidence should be estimated using the cumulative incidence function instead of the Kaplan-Meier method.
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A nonmathematical illustration of competing risk analysis Overestimation of the cumulative incidence of the outcome of interest has both practical and public health implications. An example of these implications is that treatment decisions by clinicians are often guided by risk prediction models. Ignoring competing risks in the development of these models could, among other things, lead to pos sible overtreatment in future patients. Limitations A limitation of the real-life data example is that in LASA, as in many cohort studies, disease information is collected at discrete follow -up visits, whereas the exact date of death is retrieved from municipality registers. It is therefore possible that we have missed some cases of incident depression (31). In addition, we could not distinguish between first - onset and recurrent depression. Because incidence of depression was based on a screening instrumen t (14), this does not necessarily indicate a clinical diagnosis, and there was no information on previous episodes. It is therefore possible that a part of the observed incidence of depression in our study represents recurrent episodes. Another limitation is that age was categorized into quartiles, which is associated with loss of information. Although there are better methods available to model nonlinear relationships (e.g., spline functions), in order not to divert attention from competing risk analysis we used categorization, which is still a widely used method in epidemiological research. Prediction model performance in the presence of competing risks The process of developing a prediction model in a competing risks framework is essentially the same as for other regression models, except that the subdistribution hazard model should be applied instead of regular Cox PH regression. The performance of a pr ediction model is usually assessed using the calibration and discrimination. A detailed proposal of how to assess calibration and discriminative capacity of a prediction model in a competing risks setting is described by Wolbers et al. (8). Competing risks in randomized controlled trials Whereas our paper focusses on competing risks in observational studies, competing risks also appear in the setting of randomized controlled trials (RCTs). A recent review of randomized controlled trials with survival outco mes that were published in four high - impact general medical journals showed that most of the studies were potentially susceptible to competing risks, but that this was not accounted for in the statistical analyses (32).
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Chapter 6 In RCTs with time -to-event outcomes, often additional effect measures that are derived from the KM survival curves, like the number needed to treat (NNT), are reported. Because the KM method overestimates the cumulative incidence in the presence of competing risks, the estimated NNT may also be biased. Therefore, to correctly estimate the NNT in the presence of competing risks, it is recommended to use a method based on the CIF (33). For multivariable analysis, the same applies for RCTs as for observational studies: the cause-specific hazard model should be used when one is interested in the effect of the intervention on the instantaneous rate of occurrence of the event of interest in subjects that are currently event free, whereas the subdistribution hazard model should be used when one is interested in the relative effect of the intervention on the cumulative incidence function (32). Software The cause-specific hazard model can be fitted with any software that can perform a Cox PH model. However, this is not the case for the CIF and the subdistribution hazard model. How to estimate the CIF in SPSS with the use of a macro is described elsewhere (18). In STATA, the subdistribution hazard model can be fitted using the stcrreg package (10). For SAS, macros for both the estimation of the CIF and the subdistribution hazard model are available (34, 35). Conclusion In conclusion, competing risks form an important issue in the analysis of survival data. Researchers should be aware of the potential problems associate d with censoring subjects when they experience a competing event. Dealing with competing risks requires careful formulation of the research question, selection of the appropriate method for data analysis, and interpretation of the results.
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Chapter 6 16. Noordzij M, Leffondre K, van Stralen KJ, Zoccali C, Dekker FW, Jager KJ. When do we need competing risks methods for survival analysis in nephrology? Nephrol Dial Transplant. 2013;28(11):2670-7. 17. Southern DA, Faris PD, Brant R, Galbraith PD, Norris CM, Knudtson ML, et al. Kaplan-Meier methods yielded misleading results in competing risk scenarios. J Clin Epidemiol. 2006;59(10):1110-4. 18. Verduijn M, Grootendorst DC, Dekker FW, Jager KJ, le Cessi e S. The analysis of competing events like cause -specific mortality --beware of the Kaplan -Meier method. Nephrol Dial Transplant. 2011;26(1):56-61. 19. Kleinbaum DG, Klein M. Survival Analysis: A Self -Learning Text. 3rd ed: Springer Science+Business Media; 2012. 20. Austin PC, Fine JP. Practical recommendations for reporting Fine -Gray model analyses for competing risk data. Stat Med. 2017;36(27):4391-400. 21. Latouche A, Allignol A, Beyersmann J, Labopin M, Fine JP. A competing risks analysis should report r esults on all cause -specific hazards and cumulative incidence functions. J Clin Epidemiol. 2013;66(6):648-53. 22. Gray RJ. A class of k -sample tests for comparing the cumulative incidence of a competing risk. The Annals of Statistics. 1988;16(3):1141-54. 23. Andersen PK, Geskus RB, de Witte T, Putter H. Competing risks in epidemiology: possibilities and pitfalls. Int J Epidemiol. 2012;41(3):861-70. 24. Haller B, Schmidt G, Ulm K. Applying competing risks regression models: an overview. Lifetime Data Anal. 2013;19(1):33-58. 25. R Core Team. R: A language and environment for statistical computing. Vienna, Austria: R Foundation for Statistical Computing; 2019. 26. Gray RJ. cmprsk: Subdistribution Analysis of Competing Risks. 2014. 27. Scrucca L, Santucci A, Ave rsa F. Competing risk analysis using R: an easy guide for clinicians. Bone Marrow Transplant. 2007;40(4):381-7. 28. Scrucca L, Santucci A, Aversa F. Regression modeling of competing risk using R: an in depth guide for clinicians. Bone Marrow Transplant. 2010;45(9):1388-95. 29. Büchtemann D, Luppa M, Bramesfeld A, Riedel -Heller S. Incidence of late -life depression: A systematic review. Journal of Affective Disorders. 2012;142(1):172- 9. 30. The ESEMeD Mhedea Investigators, Alonso J, Angermeyer MC, Bernert S, Bruffaerts R, Brugha TS, et al. Prevalence of mental disorders in Europe: results from the European Study of the Epidemiology of Mental Disorders (ESEMeD) project. Acta Psychiatrica Scandinavica. 2004;109(s420):21-7.
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A nonmathematical illustration of competing risk analysis 31. Binder N, Blümle A, Balmford J, Mot schall E, Oeller P, Schumacher M. Cohort studies were found to be frequently biased by missing disease information due to death. Journal of Clinical Epidemiology. 2019;105:68-79. 32. Austin PC, Fine JP. Accounting for competing risks in randomized controll ed trials: a review and recommendations for improvement. Stat Med. 2017;36(8):1203-9. 33. Gouskova NA, Kundu S, Imrey PB, Fine JP. Number needed to treat for time -to- event data with competing risks. Stat Med. 2014;33(2):181-92. 34. Kohl M, Plischke M, Leffondre K, Heinze G. PSHREG: a SAS macro for proportional and nonproportional subdistribution hazards regression. Comput Methods Programs Biomed. 2015;118(2):218-33. 35. Rosthøj S, Andersen PK, Abildstrom SZ. SAS macros for estimation of the cumulative incidence functions based on a Cox regression model for competing risks survival data. Computer Methods and Programs in Biomedi cine. 2004;74(1):69-75.
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General discussion In a systematic review from 2013, 53 papers were identified in high -impact general medical journals that adjusted for the continuous confounder age (3). In 40 of those, age was included as a covariate in the regression model. Only 13 of those explicitly reported how age was included as the model (e.g., as a linear term, as a categorized variable or with the use of higher -order terms). For the other 27 studies it was u nclear how the relation between age and the outcome was modelled. Like us, Groenwold et al. concluded that the impact of misspecification of the functional form depends on the strength of the a ssociation between the confounder and both the exposure and the outcome. In addition, they identified the distribution of the confounder, other confounders that are also adjusted for and the extent of departure from linearity as factors that influence the magnitude of bias. A cross -sectional survey from 2002 on the frequency and adequacy of adjustment for confounding found that 45% of the included papers did not explicitly report how multicategorical or continuous variables were adjusted for in the analysis (4). Failing to provide information on the assessment or modelling of continuous confounders complicates the assessment of the validity and the interpretation of the results. To increase transparency on the risk of additional bias, researchers should rep ort how the functional form of the confounder -exposure and confounder-outcome associations was assessed and taken into account. In 2007, the STROBE (Strengthening the Reporting of Observational Studies in Epidemiology) initiative published a checklist, the aim of which was to improve the quality of reporting of observational studies (5, 6) . The checklist contains 22 items, a number of which are about bias. Item number 9 emphasizes that researchers should asses the likelihood of relevant biases and should di scuss, and if possible, estimate, the direction and magnitude of bias. Item numbers 12 and 16 address confounding: researchers should make clear which confounders were adjusted for and why they were included, and which statistical methods were used to cont rol for confounding. A systematic review from 2008 on the reporting of confounding in observational studies on medical interventions found that the quality was very poor (7). For example, only 10% of the articles reported reasons for the selection of potential confounders. A more recent study from 2016 assessed whether the reporting of confounding improved after publication of the STROBE checklist (8). They found that although the quality improved in certain aspects, the overall quality remained substanda rd. Transparent reporting also includes reporting the methods used to select confounders to adjust for. A review from
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General discussion interpreted (3). Linear - and restricted cubic spline regres sion result in good approximations of the true effect. For restricted cubic spline regression, adding higher order terms further increases the flexibility of the model. However, again, this is at the expense of the interpretation of the coefficients. Although spline regression is easy to implement with most statistical software programs, most papers on spline functions present these as complex mathematical functions (16- 18). We presented spline functions in a step-by-step and non-mathematical way and focused on the application of the methods and on the interpretation of the results. In our study we illustrated the application of spline -models within a linear regression context. However, spline functions can be applied beyond standard linear regression models, for example in mediation models or in the analysis of longitudinal data. Noncollapsibility To determine which confounders to adjust for in the analysis, researchers often use the change-in-estimate criterion: they compare exposure effect estimates between a univariable- and a multivariable regression model and use an arbitrary cut -off value to determine the presence of relevant confounding (19-21). However, in logistic regression, the change -in-estimate might not only represent confounding bias but also a noncollapsibility effect. This noncollapsibility effect stems from a change in scales that occurs in logistic regression when variables are added to the model (20, 22, 23) . As a result, negative effects become more negative, and positive effects be come more positive. Thus, relying on the change-in-estimate might lead to wrong conclusions about the presence and magnitude of confounding bias (19). Using a Monte Carlo simulation study, in chapter 4 of this thesis we found that depending on the sign and magnitude of the confounding bias and the noncollapsibility effect, the change-in-estimate may under- or overestimate the magnitude of the confounding bias. Because of the noncollapsibility effect, multivariable regression analysis and IPW – two often used confounder-adjustment methods – return different but both valid estimates of the confounder-adjusted exposure effect. Multivariable regression analysis results in a conditional exposure effect estimate (24, 25) , whereas IPW results in a population - average exposure effect estimate (24-27). It is often suggested to report a population - average effect if the target population is the entire study population, while a conditional exposure effect should be reported if the target population is a subset of the st udy population (20, 22, 24 -26, 28, 29) . Although the exact differences between the effect
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Chapter 7 estimates and their respective interpretations remain unclear, it is important to consider these differences in the interpretation of the results as the populations a bout which inferences are made differ from each other. If one is unaware of the fact that multivariable regression analysis and IPW result in different exposure effect estimates with their own conclusions, conditional effects may be interpreted as population-average effects, and vice versa. Therefore, researchers should inform their choice for a confounder-adjustment method based on whether they are interested in conditional or population-average effects. Noncollapsibility effects do not only occur in logistic regression: similar to the odds ratio, the hazard ratio also suffers from noncollapsibility. As a result, the change-in-estimate criterion should not be used to determine the presence of relevant confounding in Cox regression either, and the populatio n-average hazard ratio differs from the conditional hazard ratio (30). To quantify confounding bias, one could look at the difference between the unadjusted and IPW confounder -adjusted exposure effect estimates (20, 31). If noncollapsibility is not taken into account, this could lead to wrong conclusions about the magnitude and direction of confounding bias. Then, researchers may unnecessarily adjust for certain variables in the analysis, or fail to adjust for variables that explain part of the exposure effect, eventually leading to wrong conclusions about the magnitude and direction of the exposure effect. To identify confounders it is generally recommended to determine the confounder set based on subject matter knowledge rather than on statistical methods. However, a recent review of studies in major epidemiological journals found that only 50% chose confounders based on prior knowledge, whereas 24% used data driven methods to select confounders (9). Thus, confounder selection based on the data is still common in epidemiological research. The same review found that the change -in-estimate criterion was the most popular data -driven method for confounder selection, which is attributed to the fact that the change-in-estimate criterion is recommended in many epidemiologic textbooks and articles (32). Causal mediation analysis Whereas a confounder does not lie in the causal pathway of the exposure on the outcome, a mediator does. With mediation analys is, the total effect of the exposure on
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General discussion the outcome can be decomposed into an indirect effect through the mediator and a direct effect after removing the influence of the mediator. While traditional mediation analysis defines and estimates the mediation ef fects in terms of regression coefficients, causal mediation analysis separates the causal effect definitions from the effect estimation (33, 34). In our study, we reviewed the regression -, simulation-, imputation- and weighting-based approaches to perform causal mediation analysis . If the mediator and outcome are both continuous, then all estimation approaches provide the same causal effect estimates (35). This is not necessarily the case if the exposure is continuous and the mediator is binary . In this sit uation, the estimates from the regression - and simulation-based approaches depend on the chosen causal contrast (i.e., the two compared values for the exposure) (33, 36, 37) . The imputation - and weighting-based approaches, on the other hand, still provide mediation effect estimates that are the same for every one unit difference in the continuous exposure variable (38). This is also reflected in the interpretation of the results: the indirect effects from the regression- and simulation-based approaches only apply to the two values selected for the causal contrast, whereas the imputation - and weighting -based approaches return average differences in the outcome for every one unit difference in the exposure through the mediator. In chapter 5 of this thesis , w e demonstrated that the differences between 1) the regression- and simulation -based approaches and 2) the imputation - and weighting - based approaches are explained by finite sample bias, meaning that bias decreases as sample size increases. The differences between the effect estimates obtained by the regression- and simulation -based approaches, and by the imputation - and weighting - based approaches in our empirical data example were thus explained by finite sample bias. The empirical data example also illustrated the importance of selecting the causal contrast based on substantive knowledge. If researchers are unaware of the difference between the estimation approaches and the role of the causal contrast in the regression- and simulation-based approaches, then the mediation effect estimates may be interpreted incorrectly. It is therefore recommended that researchers inform their choice for an estimation method based on whether they are interested in average effects or in effects that correspond to specific exposure values. For the regression - and simulation -based approaches, failing to consider the correct causal contrast may lead to an over- or underestimation of the true indirect effect for an individual with certain exposure values.
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Chapter 7 Although in the past decade causal mediation analysis gained in popularity, a recent scoping review found that most studies (70.7%) still apply traditional mediation analysis (39-41). In traditional mediation analysis, the indirect effect is defined and es timated using the pr oduct-of-coefficients method or the difference-in-coefficients method (42). With the product-of-coefficients method, the indirect effect is calculated as the product of the exposure -mediator and mediator -outcome e ffect, while with the d ifference-in- coefficients method the indirect effect is calculated as the difference between the total exposure-outcome effect and the direct exposure -outcome effect adjusted for the mediator. These methods provide the same indirect effect estimates if the outcome and the mediator are both continuous (43, 44). However, if the mediator is a binary variable and the exposure-mediator effect is estimated using logistic regression, then this is no longer the case. In this situation, the product-of-coefficients method should not be used to estimate the indirect effect. This is due to a mismatch in the scales on which the effects are estimated (i.e., the exposure -mediator effect is estimated on the log -odds scale, whereas the mediator-outcome effect is estimated using a linear model) (45, 46). Because this mismatch in scales does not occur with the difference -in-coefficients method (i.e., the total exposure-outcome effect and the direct exposure -outcome effect adjusted for the mediator are estimated on the same scal e), this method provides indirect effect estimates similar to the imputation - and weighting -based approaches. However, for models with a binary or time -to-event outcome that are analyzed using logistic - or Cox regression, the difference in coefficients may not only reflect the indirect effect but also a noncollapsibility effect (22, 47, 48) . Like the change -in-estimate, the difference -in- coefficients is computed as the difference between nested regression models. Failing to take a possible noncollapsibility effect into account may result in biased conclusions about the magnitude of the indirect effect. Rijnhart et al. advise d to use the potential outcomes framework or the product -of-coefficients method to estimate the indirect effect when mediation analysis is based on logistic regression analysis (49). Of the studies included in the review, only 13.2% used causal mediation analysis, and of those studies most (more than 70%) used the regression - and simulation -based approach (39). It has been recommended tha t, to ensure a causal interpretation of the mediation effects, researchers apply causal mediation analysis. In addition, the uptake of causal mediation analysis could be enhanced through tutorial papers (39, 50). With our study on the influence of the esti mation approaches and the chosen causal contrast on the mediation effect estimates and their interpretations we hope to have provided
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General discussion researchers with such a tutorial. Valente et al. provide software code of causal mediation analysis in software programs commonly used by epidemiologists (35). Competing risk analysis Survival data is often encountered in epidemiologic studies. With survival data, the time till the occurrence of the event of interest is taken into account. Competing events (i.e., events that prevent the event of interest from happening) are an important feature of survival data (51), but are often ignored and individuals that experience a competing event get censored. Conventional methods used in the analysis of survival data such as Cox regression make the assumption of independent or noninformative censoring, meaning that individuals who are censored have the same future risk of the event of interest as the individuals that remain under observation (52, 53). Naturally, censoring individuals that experience a competing event violates this assumption, and failing to account for competing risks generally results in an overestimation of the true effect o f the exposure on the outcome (52, 54-58). In chapter 6 of this thesis, we illustrated that, in the presence of competing risks, the cumulative incidence should be estimated using the cumulative incidence function (CIF) instead of the Kaplan -Meier method. To answer etiologic research questions, cause -specific hazard regression could be used, whereas subdistribution hazard regression could be used to answer prognostic research questions (51, 56, 58-60). The extent to which the cumulative incidence is overes timated if competing risks are ignored is related to the proportion of individuals experiencing the event of interest and the competing event. In our study we illustrated the methods using a geriatric population, in which the proportion of individuals expe riencing the competing event (i.e., death before the onset of depression) was high compared to the proportion of individuals experiencing the event of interest (i.e., incident depression). As a result, the cumulative incidence was greatly overestimated usi ng marginal analysis methods. Because of the older age and comorbidities, the competing risk of death is especially high in geriatric study populations (55, 58). When mortality is high, such as in geriatric populations, the overestimation of the cumulative incidence of the event of interest may be substantial. As successful improvements in health care for older adults partly relies on accurate reporting of the incidence and predictors of disease (55), it is important that the competing risk of death is acco unted for by applying specific competing risk analysis. Ignoring competing events could, for example, lead to overtreatment in future patients (58, 61). In 2012, Koller et al. examined how competing risk issues were treated in high -
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Chapter 7 impact medical journals (58). They selected 50 articles in which competing risks were present. In only 20% of the studies specific competing risk methodology was applied. This shows that a better recognition and understanding of competing events and the importance of applying competing risk analysis is needed. Although there is a clear distinction between cause -specific hazard regression and subdistribution hazard regression, it is recommended to fit models for both the event of interest and the competing event, and to apply both regression techniques for complete understanding. In addition, it is advised to use clear terminology to avoid confusion about the hazard (cause-specific versus subdistribution) presented (62, 63). Simulation studies In chapters 2, 4 and 5 of this thesis, Monte Carlo simulation studies were used. Simulation studies allow for the assessment of the performance of a method in relation to the 'true' effect. This way, bias can be quantified and expressed, among other things , in terms of absolute and relative bias (64, 65). Other performance measures that are often used are accuracy and coverage. Collins et al. emphasized the importance of examining multiple performance measures, as results may vary across measures (66). Accu racy is often expressed in terms of the mean squared error, which incorporates both bias and variability. Coverage is the proportion of times the confidence interval contains the 'true' effect. For 95% confidence intervals, the simulated confidence interva ls should contain the 'true' effect in approximately 95% of the samples. Over -coverage suggests that the results are conservative, whereas under -coverage leads to incorrect significant results (66). Because in simulation studies the 'true' effect is known, statistical methods can be compared to each other under different scenarios. Subsequently, statements can be made about which method is best to use under which circumstances. In 2006, Burton et al. conducted a small review of articles that contained si mulation studies (64). They concluded that the majority of the articles did not provide sufficient details to allow for exact replication of the simulation study. To enable the results to be reproduced, studies should include details of all simulation step s and procedures, including justification for the choices made. Most epidemiological journals actively encourage authors to make software code for the simulation study available and require the inclusion of a data availability statement in articles. The co de for the simulation studies in this thesis are included in the appendices, which allows for the replication of
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General discussion our studies. Detailed tutorials on the design, analysis, reporting and presentation of simulation studies can be found elsewhere (64, 65). Directed Acyclic Graphs In some chapters of this thesis, directed acyclic graphs (DAGs) are used to illustrate the assumed relations among variables. DAGs are causal diagrams: an arrow connecting two variables indicates that there is a causal relation. Using DAGs, researchers can determine how an exposure -outcome effect may change when adjusting for different covariates, and thus which variables to adjust for (67, 68) . In addition, DAGs can be used to distinguish between a confounder, a mediator and a collider (69). Whereas confounding requires the application of confounder-adjustment methods to obtain unbiased results, adjusting for colliders introduces bias (69, 70) and adjusting for mediators results in direct exposure-outcome effect estimates (71). Moreover , DAGs are not bound by the data available, i.e., DAGs can also contain unmeasured variables. Th ey therefore also provide insight into any residual confounding by confounders that are not included in the statistical model. DAGs have been increasingly popu lar in health research but reporting is often inconsistent. Tennant et al. provide several recommendations to improve the transparency and utility of DAGs in future research (72). Because the DAGs in this thesis only contain the variables that were inclu ded in the empirical data examples, they are simplified representations of the relations between the variables. In reality, the relations will be more complex, and the actual DAGs will contain more confounders, mediators or colliders. Concluding remarks Although regression models are commonly used in epidemiological research to estimate exposure effects, researchers often do not consider the many different ways in which bias can occur. In this thesis, we reviewed four different potential sources of bias in regression analysis, and we proposed solutions where possible. For each topic, the theory was illustrated using an empirical data example and, if applicable, simulation code was provided to reinforce understanding. To avoid bias, it is recommended that researchers consider the potential sources in the pre -analysis phase. This includes, for example, the type of effect they are interested in, the functional form of associations and the presence of competing risks in survival data. If necessary, researchers s hould adapt
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Chapter 7 their analysis, for example by explicitly modelling non -linear associations or by applying specific competing risk analysis. In addition, it is recommended to transparently report the measures taken to reduce bias and to carefully interpret the results, taking any remaining bias into consideration. Transparent reporting includes facilitating reproducibility by making software code available to readers and fellow researchers. Finally, I believe that the field of epidemiology would benefit from more non-technical and non-mathematical papers on advanced topics, as I aimed to contribute to with this thesis.
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Chapter 7 13. Lash TL, VanderWeele TJ, Haneuse S, Rothman KJ. Modern Epidemiology. 4 ed: Wolters Kluwer; 2020. 14. Bennette C, Vickers A. Against quantiles: categorization of continuous variables in epidemiologic research, and its discontents. BMC Medical Research Methodology. 2012;12(1):21. 15. Royston P, Ambler G, Sauerbrei W. The use of fractional polynomials to model continuous risk variables in epidemiology. International Journal of Epidemiology. 1999;28(5):964-74. 16. de Boor CR. A Practical Guide to Splines: Springer-Verlag New York; 1978. 17. Durrleman S, Simon R. Flexible regression models with cubic splines. Statistics in Medicine. 1989;8(5):551-61. 18. Smith PL. Splines As a Useful and Convenient Statistical Tool. The American Statistician. 1979;33(2):57-62. 19. Miettinen OS, Cook EF. Confounding: essence and detection. American Journal of Epidemiology. 1981;114(4):593-603. 20. Pang M, Kaufman JS, Platt RW. Studying noncollapsibility of the odds ratio with marginal structural and logistic regression models. Stat Methods Med Res. 2016;25(5):1925-37. 21. Kleinbaum DG, Sullivan KM, Barker ND. A Pocket Guide to Epidemiology: Springer Science + Business Media, LLC; 2007. 22. Mood C. Logistic Regression: Why We Cannot Do What We Think We Can Do, and What We Can Do About It. European Sociological Review. 2009;26(1):67-82. 23. Greenland S, Robins JM. Identifiability, exchangeability, and epidemiological confounding. Int J Epidemiol. 1986;15(3):413-9. 24. Daniel R, Zhang J, Farewell D. Making apples from oranges: Comparing noncollapsible effect estimators and their standard errors after adjustment for different covariate sets. Biom J. 2020. 25. Hernan MA, Clayton D, Keiding N. The Simpson's paradox unraveled. Int J Epidemiol. 2011;40(3):780-5. 26. Breen R, Karlson KB, Holm A. Total, Direct, and Indirect Effects in Logit and Probit Models. Sociological Methods & Research. 2013;42(2):164-91. 27. Burgess S. Estimating and contextualizing the attenuation of odds ratios due to non collapsibility. Communications in Statistics - Theory and Methods. 2016;46(2):786-804. 28. Karlson KB, Popham F, Holm A. Marginal and Conditional Confounding Using Logits. Sociological Methods & Research. 2021:0049124121995548.
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General discussion 29. Zhang Z. Estimating a Marginal Causal Odds Ratio Subject to Confounding. Communications in Statistics - Theory and Methods. 2008;38(3):309-21. 30. Martinussen T, Vansteelandt S. On collapsibility and confounding bias in Cox and Aalen regression models. Lifetime Data Analysis. 2013;19(3):279-96. 31. Janes H, Dominici F, Zeger S. On quantifying the magn itude of confounding. Biostatistics. 2010;11(3):572-82. 32. Talbot D, Diop A, Lavigne -Robichaud M, Brisson C. The change in estimate method for selecting confounders: A simulation study. Statistical Methods in Medical Research. 2021;30(9):2032-44. 33. Imai K, Keele L, Tingley D. A general approach to causal mediation analysis. Psychol Methods. 2010;15(4):309-34. 34. Muthén BO, Muthén LK, Asparouhov T. Regression and Mediation Analysis using Mplus. Los Angeles, CA: Muthén & Muthén; 2017. 35. Valente MJ, Rijnhart JJM, Smyth HL, Muniz FB, MacKinnon DP. Causal Mediation Programs in R, Mplus, SAS, SPSS, and Stata. Struct Equ Modeling. 2020;27(6):975-84. 36. VanderWeele TJ. Explanation in Causal Inference: Methods for Mediation and Interaction: Oxford University Press; 2015. 37. Valeri L, VanderWeele TJ. Mediation Analysis Allowing for Exposure –Mediator Interactions and Causal Interpretation: Theoretical Assumptions and Implementation With SAS and SPSS Macros. Psychological Methods. 2013;18(2):137-50. 38. Steen J, Loeys T, Moerkerke B, Vansteelandt S. medflex: An R Package for Flexible Mediation Analysis using Natural Effect Models. Journal of Statistical Software. 2017;76(11). 39. Rijnhart JJM, Lamp SJ, Valente MJ, MacKinnon DP, Twisk JWR, Heymans MW. Mediation analysis methods used in observational research: a scoping review and recommendations. BMC Medical Research Methodology. 2021;21(1):226. 40. Vo T -T, Superchi C, Boutron I, Vansteelandt S. The conduct and reporting of mediation analysis in recently publish ed randomized controlled trials: results from a methodological systematic review. Journal of Clinical Epidemiology. 2020;117:78-88. 41. Rizzo RRN, Cashin AG, Bagg MK, Gustin SM, Lee H, McAuley JH. A Systematic Review of the Reporting Quality of Observation al Studies That Use Mediation Analyses. Prevention Science. 2022.
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Chapter 7 42. VanderWeele TJ. Mediation Analysis: A Practitioner's Guide. Annual Review of Public Health. 2016;37(1):17-32. 43. MacKinnon DP, Valente MJ, Gonzalez O. The Correspondence Between Causal and Traditional Mediation Analysis: the Link Is the Mediator by Treatment Interaction. Prevention Science. 2020;21(2):147-57. 44. Rijnhart JJM, Twisk JWR, Chinapaw MJM, de Boer MR, Heymans MW. Comparison of methods for the analysis of relatively simple mediation models. Contemporary Clinical Trials Communications. 2017;7:130-5. 45. Rijnhart JJM, Valente MJ, Smyth HL, MacKinnon DP. Statistical Mediation Analysis for Models with a Binary Mediator and a Binary Outcome: the Differences Between Causal and Traditional Mediation Analysis. Prevention Science. 2021. 46. Li Y, Schneider JA, Bennett DA. Estimation of the mediation effect with a binary mediator. Statistics in Medicine. 2007;26(18):3398-414. 47. MacKinnon DP, Lockwood CM, Brown CH, Wang W, Hoffman JM. Th e intermediate endpoint effect in logistic and probit regression. Clinical Trials. 2007;4(5):499-513. 48. Jiang Z, VanderWeele TJ. When Is the Difference Method Conservative for Assessing Mediation? American Journal of Epidemiology. 2015;182(2):105-8. 49. Rijnhart JJM, Twisk JWR, Eekhout I, Heymans MW. Comparison of logistic - regression based methods for simple mediation analysis with a dichotomous outcome variable. BMC Medical Research Methodology. 2019;19(1):19. 50. Vo T -T, Cashin A, Superchi C, Tu PHT, Ng uyen TB, Boutron I, et al. Quality assessment practice in systematic reviews of mediation studies: results from an overview of systematic reviews. Journal of Clinical Epidemiology. 2022;143:137 - 48. 51. Geskus RB. Data Analysis with Competing Risks and Inte rmediate States. Boca Raton, FL: Taylor & Francis Group, LLC; 2016. 52. Putter H, Fiocco M, Geskus RB. Tutorial in biostatistics: competing risks and multi-state models. Stat Med. 2007;26(11):2389-430. 53. Austin PC, Lee DS, Fine JP. Introduction to the an alysis of survival data in the presence of competing risks. Circulation. 2016;133(6):601-9. 54. Satagopan JM, Ben-Porat L, Berwick M, Robson M, Kutler D, Auerbach AD. A note on competing risks in survival data analysis. Br J Cancer. 2004;91(7):1229-35. 55. Berry SD, Ngo L, Samelson EJ, Kiel DP. Competing risk of death: an important consideration in studies of older adults. J Am Geriatr Soc. 2010;58(4):783-7.
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General discussion 56. Lau B, Cole SR, Gange SJ. Competing risk regression models for epidemiologic data. Am J Epidemiol. 2009;170(2):244-56. 57. Wolbers M, Koller MT, Witteman JC, Steyerberg EW. Prognostic models with competing risks: methods and application to coronary risk prediction. Epidemiology. 2009;20(4):555-61. 58. Koller MT, Raatz H, Steyerberg EW, Wolbers M. Com peting risks and the clinical community: irrelevance or ignorance? Stat Med. 2012;31(11-12):1089-97. 59. Andersen PK, Geskus RB, de Witte T, Putter H. Competing risks in epidemiology: possibilities and pitfalls. Int J Epidemiol. 2012;41(3):861-70. 60. Fine JP, Gray RJ. A proportional hazards model for the subdistribution of a competing risk. Journal of the American Statistical Association. 1999;94(446):496-509. 61. Steyerberg EW. Clinical Prediction Models: A Practical Approach to Development, Validation, and Updating: Springer-Verlag New York; 2009. 62. Latouche A, Allignol A, Beyersmann J, Labopin M, Fine JP. A competing risks analysis should report results on all cause -specific hazards and cumulative incidence functions. J Clin Epidemiol. 2013;66(6):648-53. 63. Wolkewitz M, Cooper BS, Bonten MJM, Barnett AG, Schumacher M. Interpreting and comparing risks in the presence of competing events. BMJ : British Medical Journal. 2014;349:g5060. 64. Burton A, Altman DG, Royston P, Holder RL. The des ign of simulation studies in medical statistics. Statistics in Medicine. 2006;25(24):4279-92. 65. Morris TP, White IR, Crowther MJ. Using simulation studies to evaluate statistical methods. Statistics in Medicine. 2019;38(11):2074-102. 66. Collins LM, Scha fer JL, Kam C -M. A comparison of inclusive and restrictive strategies in modern missing data procedures. Psychological Methods. 2001;6(4):330-51. 67. Shrier I, Platt RW. Reducing bias through directed acyclic graphs. BMC Medical Research Methodology. 2008;8(1):70. 68. Hernan MA, Robins JM. Causal Inference: What If. Boca Raton: Chapman & Hall/CRC; 2020. 69. Pearl J. Causality. 2 ed: Cambridge University Press; 2009. 70. Cole SR, Platt RW, Schisterman EF, Chu H, Westreich D, Richardson D, et al. Illustrating bias due to conditioning on a collider. International journal of epidemiology. 2010;39(2):417-20.
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Chapter 7 71. Schisterman EF, Cole SR, Platt RW. Overadjustment bias and unnecessary adjustment in epidemiologic studies. Epidemiology (Cambridge, Mass). 2009;20(4):488-95. 72. Tennant PWG, Murray EJ, Arnold KF, Berrie L, Fox MP, Gadd SC, et al. Use of directed acyclic graphs (DAGs) to identify confounders in applied health research: review and recommendations. International journal of epidemiology. 2021;50(2):620-32.
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English summary result, the difference between univariable - and multivariable exposure effect estimates may not only represent confounding bias but also a noncollap sibility effect. Depending on the sign and magnitude of the confounding bias and the noncollapsibility effect, the change-in-estimate may under - or overestimate the magnitude of confounding bias. Because of the noncollapsibility effect, multivariable regre ssion analysis and inverse probability weighting return different but valid estimates of the confounder -adjusted exposure effect, with their own respective interpretations. Ideally the set of confounders is determined in the study design phase and based on subject-matter knowledge. To quantify confounding bias, one could compare the unadjusted exposure effect estimate and the estimate from an inverse probability weighted model. Causal mediation analysis A mediator explains the effect of the exposure on the outcome, as the exposure causes the mediator, and the mediator in turn causes the outcome. Instead of adjusting for a mediator, mediation analysis can be used to decompose the total effect of the exposure on the outcome into an indirect effect through th e mediator and a direct effect after removing the influence of the mediator. With causal mediation analysis, the causal mediation effects can be estimated using different approaches, including regression, simulation, imputation and weighting. Chapter 5 shows that, if the exposure is continuous and the mediator is binary, then the different estimation approaches do not provide the same effect estimates. For these models, the regression - and simulation -based approaches require the selection of a causal contrast, i.e., the values chosen for the exposure. As a result, the regression - and simulation-based approaches return effects that correspond to specific exposure values, whereas the imputation - and weighting -based approach es return overall effects. If researchers are unaware of the differences between the approaches and the role of the causal contrast in the regression- and simulation-based approaches, then the mediation effect estimates may be interpreted incorrectly. Competing risks Conventional methods for the analysis of survival data make the assumption of independent or noninfo rmative censoring, meaning that individuals who are censored have the same future risk of the event of interest as individuals that remain under observation. This assumption is not met if individuals who experience a competing event, i.e., an event that prevents the event of interest from happening, are censored. Therefore,
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English summary competing risk analysis should be applied to analyse survival data in the presence of competing risks. Chapter 6 shows that, in the presence of competing risks, the cumulative inciden ce should be estimated using the cumulative incidence function (CIF). Using marginal methods such as the Kaplan-Meier method results in an overestimation of the cumulative incidence. The extent to which the cumulative incidence is overestimated is related to the proportion of individuals that experience the event of interest and the competing event. To answer etiologic and prognostic research questions, cause-specific hazard regression and subdistribution hazard regression can be used. In cause-specific hazard regression individuals that experience a competing event are removed from the risk set, whereas they remain in the risk set in subdistribution hazard regression. As a result, the cause - specific hazard is quantified among individuals that are at risk of developing the event of interest, but the subdistribution hazard has no straightforward interpretation. Therefore, the subdistribution hazard should only be used to estimate the incidence of the event of interest taking the competing risks into account. D ealing with competing risks requires careful formulation of the research question (etiologic vs. prognostic), selection of the appropriate method for data analysis and interpretation of the results. In addition, it is suggested to use both regression models and present the results for all causes for complete understanding. Conclusion Although regression models are commonly used in epidemiological research to estimate exposure effects, researchers do often not consider the many different ways in which bias can occur. In this thesis, I reviewed four different potential sources of bias in regression analysis, and proposed solutions where possible. To avoid bias, it is recommended that researchers consider the potential sources in the pre-analysis phase and ada pt their analysis if necessary. In addition, it is recommended to transparently report the measures taken to reduce bias and to carefully interpret the results, taking any remaining bias into consideration. Finally, I believe that the field of epidemiology would benefit from more non -technical and non -mathematical papers on advanced topics, as I aimed to contribute to with this thesis.
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Nederlandse samenvatting Achtergrond Epidemiologen zijn hoofdzakelijk geïnteresseerd in het effect van een determinant op een uitkomst. Dit zogenaamde determinant -uitkomst effect wordt vaak geschat met behulp van regressieanalyse, waarbij de determinant wordt gerelateerd aan de uitkomst. De verdeling van de uitkomst bepaalt welke regressi etechniek het meest gepast is om het determinant-uitkomst effect zo nauwkeurig mogelijk te schatten. In epidemiologisch onderzoek worden lineaire (voor continue uitkomsten), logistische (voor dichotome uitkomsten) en Cox regressie (voor survival uitkomsten) het meest toegepast. Het doel van onderzoek is om het werkelijke effect van de determinant op de uitkomst te isoleren, maar vaak is het verband tussen een determinant en een uitkomst niet volledig toe te schrijven aan de determinant, oftewel, het effec t is vertekend. Deze vertekening wordt ook wel bias genoemd. Wanneer bias niet volledig geëlimineerd wordt is het geschatte effect geen goede weergave van het werkelijke onderliggende effect. Dit kan bijvoorbeeld leiden tot beïnvloeding van de klinische be sluitvorming en onder - of overbehandeling van patiënten. Doel In dit proefschrift beschrijf ik op niet-technische en niet -wiskundige wijze verschillende situaties waarin bias kan optreden in regressieanalyse, en draag ik waar mogelijk oplossingen aan om deze bias te voorkomen. De focus ligt op vier mogelijke bronnen van bias: de schatting van niet-lineaire effecten, noncollapsibility, causale mediatie-analyse en competing risks. In elk hoofdstuk wordt de theorie geïllustreerd aan de hand van data van de Longitudinal Aging Study Amsterdam of van het Amsterdamse Groei en Gezondheids Onderzoek. Sommige hoofdstukken bevatten tevens een simulatiestudie om de prestaties van modellen te evalueren en methoden onderling te vergelijken. Niet-lineaire effecten Een belangrijke aanname van lineaire, logistische en Cox regressie is dat de determinant lineair gerelateerd is aan de uitkomst. Wanneer deze aanname wordt geschonden is de effectschatting geen goede weergave van het werkelijke onderliggende effect en word t er bias geïntroduceerd. Een confounder is een variabele die gerelateerd is aan zowel de determinant als de uitkomst en die niet ligt in het causale pad tussen beiden. Hierdoor vertekent een confounder het determinant -uitkomst effect. Veel onderzoekers zijn zich er bij het corrigeren voor confounding niet van bewust dat deze lineariteitsaanname niet alleen van toepassing is op het determinant-uitkomst effect, maar ook op de confounder-
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Nederlandse samenvatting hiervan schatten regressie en simulatie effecten die horen bij deze determinantwaarden, terwijl imputatie en weging algemene effecten schatten. Als onderzoekers zi ch niet bewust zijn van de verschillen tussen deze methoden en van de rol van het causale contrast bij regressie en simulatie kunnen de mediatie-effecten o njuist worden geïnterpreteerd. Competing risks Conventionele methoden voor de analyse van survival data gaan uit van onafhankelijke of niet -informatieve censoring. Dit betekent dat personen die gecensored worden hetzelfde toekomstige risico op een bepaalde uitkomst hebben als personen die niet gecensored worden. Aan deze aanname wordt niet voldaan wanne er personen die een competing event meemaken, d.w.z. een event dat ervoor zorgt dat de uitkomst niet meer kan optreden, worden gecensored. Om bias te voorkomen kan survival data , in de aanwezigheid van competing risks, geanalyseerd worden met competing risk analyse. Hoofdstuk 6 laat zien dat, in het geval van competing risks , de cumulatieve incidentie geschat moet worden met behulp van de cumulatieve incidentiefunctie (CIF). Het gebruik van conventionele methoden zoals de Kaplan -Meier methode resulteert i n een overschatting van de cumulatieve incidentie. De mate van deze overschatting hangt af van de verhouding tussen individuen die over de tijd de uitkomst ontwikkelen en individuen die een competing event meemaken. Om etiologische en prognostische onderzoeksvragen te beantwoorden, kunnen cause- specific hazard regressie en subdistribution hazard regressie gebruikt worden. Bij cause- specific hazard regressie worden de individuen die een competing event meemaken verwijderd uit de studie, terwijl deze bij subdistribution hazard regressie juist deel blijven uitmaken van de studie. Als gevolg hiervan berekent de cause-specific hazard het risico op de uitkomst voor individuen die hier nog gevaar voor lopen, maar heeft de subdistribution hazard geen eenduidige interpretatie. Daarom dient de subdistribution hazard enkel te worden gebruikt om, rekening houdend met de competing risks, de incidentie van de uitkomst te schatten. De aanwezigheid van competing risks in een studie ver eist een zorgvuldige formulering van de onderzoeksvraag (etiologisch vs. prognostisch), selectie van de juiste methode om de data te analyseren en een juiste interpretatie van de resultaten. Bovendien wordt aanbevolen om beide regressiemodellen te gebruike n en voor de volledigheid de resultaten voor zowel de uitkomst als de competing events te presenteren.
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Nederlandse samenvatting Conclusie Hoewel regressiemodellen vaak gebruikt worden in epidemiologisch onderzoek om determinant-uitkomst effecten te schatten houden onderzoekers vaa k geen rekening met de vele verschillende manieren waarop bias kan optreden. In dit proefschrift heb ik vier mogelijke bronnen van bias in regressieanalyse beschreven en waar mogelijk oplossingen aangedragen. Om bias te voorkome n wordt aanbevolen dat onder zoekers kritisch nadenken over mogelijke bronnen van bias voordat zij hun data analyseren en zo nodig hun analyse aanpassen. Daarnaast wordt aanbevolen om transparant te rapporteren over de maatregelen die zijn genomen om bias te verminderen en om de resultaten zorgvuldig te interpreteren, daarbij rekening houdend met eventuele resterende bias . Ter afsluiting ben ik er van overtuigd dat de epidemiologie baat zou hebben bij meer niet -technische en niet -wiskundige artikelen over complexe onderwerpen, waar ik met dit proefschrift gepoogd heb aan bij te dragen.
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PhD portfolio Courses Year ECTs Research Integrity, Amsterdam UMC Doctoral School 2021 2 Medische Basiskennis, EpidM 2021 8 Data Processing, University of Amsterdam 2020 6 Scientific Programming 2, University of Amsterdam 2019 3 Scientific Programming 1, University of Amsterdam 2019 3 Regressietechnieken, EpidM 2018 5 Longitudinale Data Analyse, EpidM 2018 3 Conferences and scientific meetings WEON 2021, online 2021 1 WEON 2019, Groningen 2019 1 rstudio::conf, Austin 2019 1.14 Intervision meetings, Amsterdam Public Health Research Institute 2018 - 2021 0.5 Supervision and teaching activities Supervision of Nine Droog, BSc Health and Life Sciences, "Has the publication of the GRoLTS-checklist improved the reporting of results of latent trajectory analyses?" 2021 1 Supervision of Rob Rekveld, BSc Health and Life Sciences, "The quality of reporting in latent trajectory studies through the years: associations with author-, journal- and study characteristics" 2021 1 Supervision of Sema Atmaca, BSc Health Sciences, "Associatie tussen fluctuaties in fysieke activiteit en lichaamsvetverdeling onder Nederlandse volwassenen" 2020 1 Supervision of Ewa Sillem, BSc Health Sciences, "Daily fluctuations in physical activity duration and its relationship with the need for recovery from work due to work-related fatigue in 42-year old adults" 2020 1 Supervision of Carolien de Visser, BSc Health Sciences, "Associaties fysieke activiteit en fluctuaties fysieke activiteit op slaapkwaliteit onder Nederlandse volwassenen" 2020 1
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PhD portfolio Teaching activities for EpidM 2018 - 2022 2.2 Teaching activities for the Department of Epidemiology and Data Science 2018 - 2022 4 Other activities Building Tidy Tools, rstudio::conf 2019 Statistical consulting through E&B Xpert 2021 - 2022 Reviewer for various international journals 2020 - 2022 Member of the WEON 2021 organization committee 2019 - 2021 Member of the APH Methodology Junior Board 2019
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About the author Noah Alexandra Schuster was born on May 5 th, 1992 in Amsterdam. After attending the Vossius Gymnasium, she went on to study for her bachelor's degree in Health Sciences at VU University in Amsterdam. She spent a semester abroad at Eötvös Loránd University in Budapest, Hungary, following courses from their master's program Health Policy, Planning and Financing. She wrote her bachelor's thesis on fluctuations in physical activity and physical fitness at the Departm ent of Methodology and Applied Biostatistics under the supervision of dr. Trynke Hoekstra. During her studies, Noah rowed for A.A.S.R. Skøll, winning medals in different boat classes at both national and international regattas. In 2016, Noah went to study Epidemiology at Utrecht University. She graduated with a double specialization in Medical Statistics and Pharmacoepidemiology. During her master's, she completed a 13-month research project under the supervision of dr. Linda Peelen and dr. Romin Pajouheshnia at the Department of Data Science and Biostatistics of the Julius Center for Health Sciences and Primary Care. This resulted in her thesis on approaches to account for time-varying treatment use in the development of prognostic models, which was publis hed in Statistica Neerlandica. After this project, she completed another 5-month research project under the supervision of prof.dr. Michael Hauptmann at the Department of Psychosocial Research and Epidemiology of the Netherlands Cancer Institute. This resu lted in a systematic review about diagnostic imaging among cancer patients. In August 2018, Noah started her PhD research on bias in regression analysis at the former Department of Epidemiology and Biostatistics at the VU University Medical Center, now the Department of Epidemiology and Data Science at the Amsterdam University Medical Center, under the supervision of prof.dr. Jos Twisk, dr. Martijn Heymans and dr. Judith Rijnhart. Alongside her PhD, she tutored multiple EpidM courses, served as a statistical consultant and was a member of the WEON 2021 organization committee. As of September 2022, Noah works as a Senior Associate Consultant at Bain & Company.
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