JAMA#
Dear Dr Muzaale:
Thank you for your review and comments on MS #JAMA24-5945, “Increasing Equity in Kidney Transplantation: Results of the Kidney Transplant Fast Track Study.” For your information, the decision for this manuscript was Reject & Refer to a JAMA Network Journal. If appropriate, comments from all reviewers to the author are included below.
Please remember that your participation in review of this manuscript, the editorial decision, and reviewer comments are all confidential and should not be shared with others.
Thank you for your assistance and participation in the review process for JAMA.
Sincerely,
Wolfgang C. Winkelmayer, MD, MPH, ScD (Pronouns: he/his/him) Associate Editor, JAMA
Dear Dr. Muzaale, thanks for taking the time top evaluate this paper for JAMA. I appreciate your insights and recommendation. Best regards, Wolfgang
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Reviewer #1: Remarks to the Author: The authors assess whether a fast-track intervention reduces time-to-waitlisting and transplantation among patients with ESKD who have been referred for transplantation
An intuitive metric to answer this question would be median time-to-event (waitlisting or transplant) in trial arm vs. historical controls, visualized in overlayed cumulative incidence functions. This would help the readers grasp the impact of the intervention (e.g. median time reduced by 3 months). Instead the authors report their findings as 40% greater chance of being placed on the active waitlist and 21% greater chance of receiving a transplant. While this is a common way of reporting, it is actually inaccurate since these percentages are comparing two numbers from an exponentiated scale. sHR=1.40 is more accurately reported as “1.4-fold higher sub hazards”. But a statement about XX% higher or XX lower should be based on the log sHRs.
Does the fast-track intervention apply only to deceased donor kidney transplantation or also to living donor transplantation? Have the authors considered “potential living donor candidates discussed and available or not-available” as a baseline predictor of time-to-event?
The study hypothesis, whether “completing testing on the same day of the first pre-transplant appointment reduces time-to-event vs. providing patients with a list of tests to complete independently”, is buried in the fourth paragraph. This should be articulated early in the introduction.
The authors misleadingly characterize their study as one addressing disparities in access to KT among all ESKD patients rather than the subset referred for KT . For instance, Schold et al. is cited in the conclusion of the discussion, but the reference is “about rates of waitlisting following ESKD onset”. The title, abstract, and discussion should make it clear that only ESKD patients referred for transplant evaluation are included. In addition to clarifying the study’s scope, the authors should avoid general statements about the healthcare system. For instance, their analysis completely neglects disparities in referral from dialysis to transplant. Their discussion of the literature does not tell us whether the disparity in the ESKD population is predominantly driven by the bottlenecks before referral tor after referral for transplantation.
Did the authors assess whether proportionality of hazards assumption was fulfilled by their models? My concern is that disparities are best captured by non-parametric survival curves that make no assumption about proportional hazards. It is entirely possible for two survival curves to criss-cross (suggesting disparities at different times) and yield a HR=1. With non-parametric curves that would be easy to see. With semi-parametric curves, what is visualized is “forced” to be proportionately separated at each time point. This is not compelling in the complex clinical setting under study, where preemptive living donation occurs rather early after referral, and mortality is quite high for those remaining on the waitlist for long
Fine and Gray methods for competing risks are most helpful when one wants to estimate cumulative incidence functions. But if descriptive failure-specific effects (death, transplant, etc) are of interest, Cox regression may yield more meaningful HRs. This is a critical point made by Lau B AJE 2009 (reference #58)
The columns for test-statistic and p-value in Table 1 are not at all informative. The authors perform multivariable regression and that should be sufficient. The readers should be allowed to focus on the two clinically meaningful column of the study arms. Additionally, all outcome reporting should be excluded from Table 1, which is traditionally used to describe the study population at baseline.
Outcomes such as “days from evaluation to any waitlisting” captured in the appropriate survival framework in the cumulative incidence curve and should NOT be reported in a table, since the table does’t make it clear how censoring is handled.
Explain how the tables/figures are inappropriate (sent to author: None
Reviewer #2: Remarks to the Author: Myakovsky et al. report on results of a single center trial to improve rates of waitlisting and kidney transplant among patients referred to the transplant center. The effect of the intervention is examined through comparison to historical controls at the same center. I commend the authors for committing the tenacity required to carry out an interventional study and I appreciate their commitment to promoting equity in transplant. In general, I am excited by the results but I think the potential for confounding is high because of the use of a historical comparator group. I have the following concerns.
Potential for unmeasured confounding with any historical control: The efficiency of transplant center operations often depend heavily on the effectiveness of a medical director, administrator and lead surgeon. The transplant rate and ‘aggressiveness’ of the center in terms of accepting patients with comorbidities or higher risk organs can change when any of these individuals leave and someone needs to be hired. For example, it is common for a transplant center to lose a surgeon, have their volumes fall, then have the volumes rise again when a new surgeon is hired. As a second example, when transplant center coordinators are short-staffed, it is very common for waitlist management to get much worse. We do not, however, have any data about center leadership or staffing in this manuscript. I do not know, for example, what “virtually the same clinical team” means • Were the center’s kidney transplant volumes similar during the periods of study here? • If one period’s transplant volume was higher than the other period, can the authors make the case that the difference was due to their intervention?
Censoring and very large differences in outcomes from Table 1: Relevant to my point above, Table 1 reveals some very large differences in outcomes that the authors should address. For example, in the intervention cohort, patients are 10 times as likely to experience the “outcome” of being declined for waitlisting and also much more likely to be declined for transplant compared to the historical controls. In a revision, the authors should explain these findings and also, address censoring clearly in the methods.
Process metrics would help the reader understand the effect of the intervention. What kind of testing was completed the same day in the earlier cohort versus the later one? Transplant candidates often need cardiac evaluation or testing (e.g. a stress test) or evaluation by an ID specialist or a hepatologist if, e.g., liver fibrosis is suspected. It would be useful to see some kind of assessment of the tests that the center managed to perform the same day. • The authors should also report on the labor required to implement the new workflow, which speaks to the potential for generalizability to other centers. A) Minor: In general, I do not think it is best practice in a manuscript to expect a reviewer to download a prior manuscript and study it to understand the methods. Instead, provide the necessary information in an appendix. In this case, specific information about the trial’s operations should be in the submitted materials.
Many epidemiologists express caution about the practice of reporting outcomes in subgroups unless the investigators first demonstrate effect modification. Did race modify the effect of the intervention on the outcomes? I do not see any formal tests of interaction in the manuscript. I would like to hear the views of a statistician on Table 2a’s comparisons. In general, the authors should consider de-emphasizing the race-specific rates, for example by taking them out of the abstract.
Relevant to #4, the argument in paragraph 3 of the discussion lacks clarity. Are the authors saying that the intervention reduced disparities between Black and White patients in terms of waitlisting and transplant? Or are they instead saying that the magnitude of the effect of the intervention appeared approximately the same in Black and White patients?
Intention to treat approach: I am unsure why the authors could not perform an intention-to-treat analysis (unadjusted) that includes patients who consented but did not come to the interview. This is best practice for trials. Further, the flow chart does not make it easy to understand how many patients did not come to the interview (n=8) versus did not come to clinic (n=166). Did these patients come to clinic at a later date?