Reading Response Discussions

Research Article Info:

Hepatology. 2014 Apr;59(4):1311-9. doi: 10.1002/hep.26920. Epub 2014 Mar 1.

Hepatitis C disease severity in living versus deceased donor liver transplant recipients: an extended observation study.

Terrault NA1, Stravitz RT, Lok AS, Everson GT, Brown RS Jr, Kulik LM, Olthoff KM, Saab S, Adeyi O, Argo CK, Everhart JE, Rodrigo del R; A2ALL Study Group.

1. Briefly summarize the study objective and design:

Objective: Compare the severity of HCV disease and risk of advanced fibrosis post-liver transplant for HCV+ organs transplanted via LDLT vs. DDLT.

Design: This study utilizes the Adult-to-Adult Living Donor Liver Transplantation Cohort (A2ALL). It is a multi-center observational cohort study aimed to compare outcomes between LDLT and DDLT recipients.

2) Consider selection into the analysis sample, including differential enrollment (from refusal to participate or differential survival up to the time of study initiation) and differential attrition of enrolled participants (from death or drop out). Did the authors describe potential selective participation/attrition? Did they describe predictors of participation/attrition? Do you think selection bias is a major potential source of bias in this study?

There sample was formed from those HCV-infected recipients who had a living donor evaluated between 1998 and 2009.

There were 513 candidates and 138 were excluded from the current analysis. Exclusion criteria included aborted LTs, establishment of pre-LT sustained virologic response (cure of HCV), being in the first 20 cases of LDLT at a particular center (since LDLT is a relatively new procedure), having graft failure within 90 days.

They don’t discuss possible differential exclusion due to graft loss since they say recurrent HCV is rare in the early post-transplant period. This is concerning to me and I think the number of LDLT/DDLT that lead to early graft loss should be an outcome investigated.

They did not describe predictors of participation and attrition. I believe that is because this is not an issue in this case. There are no obvious reasons why a study participant would differentially participate or drop out of the study amongst the DDLT vs. LDLT.

My potential concerns for selection bias would stem from different centers with generally different outcomes differentially contributing more LD vs. DD transplants. I’d expect this to skew the results. My other concern is that the exclusion criteria skewed the results – particularly the immediate graft failures being excluded.

Though I

3) Now imagine a hypothetical trial to test the hypothesis of the observational study you selected (this is a thought experiment—time and money are no issue for your hypothetical trial). When would you enroll participants, randomize participants, and assess the outcome to minimize selection bias?

It would be difficult to imagine a trial where it would be possible to randomize participants to a living donor transplant vs. deceased donor transplant. You’d have to utilize patients that came for evaluation of LDLT as in this study and then randomize them to either LD or DD LT. Although this might be ethical since this study supports the fact that they may be equivalent options, that would be operating under the assumption that the living donor is a good fit for everyone and that there would be an appropriate deceased donor available. After thinking about it, this would not be ethically feasible under the current logistics. However, if you could somehow make the logistics work out, I’d enroll anyone coming in for a LD evaluation that is a good fit, and randomize them to either receive an LD/DD LT. I would do a cluster RCT. 

1) Briefly summarize the study objective and design.

The study objective was to test the impact of the Earned Income Tax Credit (EITC) on child development. The authors used data from the National Longitudinal Survey of Youth during 1886-2000 to test effects on Behavioral Problems Index and Home Observation Measurement of the Environment inventory scores. They did two things: 1) a multivariate linear regression with child-level fixed effects to test association of EITC payment size with child development scores, and 2), an IV analysis using EITC payment size as an instrument to estimate the associations of income with child development measures.

2) Consider selection into the analysis sample, including differential enrollment (from refusal to participate or differential survival up to the time of study initiation) and differential attrition of enrolled participants (from death or drop out). Did the authors describe potential selective participation/attrition? Did they describe predictors of participation/attrition? Do you think selection bias is a major potential source of bias in this study?

The authors do mention that missing data were associated with lower income, Black participants, which they dealt with using multiple imputation. Though they were referring to people enrolled in the study, it is possible that this same association would be seen among people who refused to participate in the first place. Additionally, they only included people who responded to the survey at least two consecutive rounds.

Selection bias is certainly a possibility. For example, we could imagine a situation where lower income (the exposure) may be associated with reluctance to participate in health research, and therefore this group could be more likely to drop out of the study. Participants whose children have behavioral problems (the outcome) could be experiencing some kind of stress or conflict in the home, which could lead to residential instability, and in turn, loss to follow up. A similar scenario could also cause selection bias at study enrollment.

3) Now imagine a hypothetical trial to test the hypothesis of the observational study you selected (this is a thought experiment—time and money are no issue for your hypothetical trial). When would you enroll participants, randomize participants, and assess the outcome to minimize selection bias?

It's probably easier to think about their first hypothesis, which is effect of EITC payment size on child development outcomes. We could take a bunch of women who've never given birth, with the authors' eligibility criteria of income <$50,000, randomize them to receive varying amounts of EITC annually, and order them all to get pregnant immediately (let's assume they all can). We could then begin assessing the child's development from the day s/he is born. 

1. Urinary, sexual and rectal morbidity were assessed before and after brachytherapy (radiation seeds for prostate cancer). This is a prospective cohort study. 

2.) The authors did not describe potential selective participation/ attrition. They just mention that as this is a single center, our patients might not represent other centers. However, this gets more at generalizability than selection bias. I think selection bias is always a possibility. All men had to have brachytherapy to get into the study, the radiation dose is depending on their cancer. Those with worse cancers or baseline erectile dysfunction (or perhaps close to it), but make men more likely to enter the study. This might elevate our measure of association. Without any mention of how patients were accrued, we cannot rule out selection bias.

3.) I think the best way to study this question would be to randomize to radiation therapy versus active surveillance and brachytherapy. The outcome of interest would be long-term erectile dysfunction. I would enroll participants as soon as they found out they had prostate cancer and might be interested in treatment (low-grade). We will then randomize to brachytherapy or control. Perhaps even we should do a sham treatment of seeds that don't contain radiation (maybe that is the better control but not sure ethical). We can then assess selection bias by seeing if we have differential drop-out (perhaps more in the control or brachytherapy group).  

Paper: Declining and rebounding unhealthy alcohol consumption during the first year of HIV care in rural Uganda, using phosphatidylethanol to augment self-report.  Addiction 2016, 111(2), 272-279.

Study design and objective: This was an observational cohort study of HIV infected patients that were newly registered at an HIV treatment clinic in Uganda.  Patients were examined and interviewed quarterly.  The objective was to assess changes in unhealthy alcohol consumption during the first year of HIV care.  It is possible that when HIV infected patients that drink at unhealthy levels enter an HIV treatment program, they could change their drinking behavior for one reason or another.

Selection issues: Inclusion criteria for this study was: Entering HIV-care at the ISS Clinic, and reporting any alcohol consumption in the past year.  The ISS clinic is a government owned HIV treatment clinic.  I think with respect to HIV-infected patients in this region, the clinic captures a fairly representative group.  They selected "any alcohol consumption", because they were interested in recruiting only drinkers.  Based on the outcome of "changes in unhealthy alcohol consumption", there could be some kind of volunteer bias.  People who are willing to participate in ongoing studies at this clinic could be people who are also more likely to comply with medical recommendations.  At this clinic, the predominant advice is likely to be telling people to abstain from alcohol.  I therefore suspect that participants in this study could be people that are more likely reduce alcohol consumption based on advice from nurses and doctors.  In general, with respect to HIV disease, HIV treatment clinics of this nature take care of survivors, because rapid progressors probably die off before coming to the clinic and going through the associated red tape.  To the extent that unhealthy alcohol consumption and changes thereof are related to HIV disease progression especially when off HIV treatment, this sample could be biased with respect to these types of questions.  But I think the sample is okay for the questions reported in this paper.

Randomized trial: One question here is whether HIV care per se changes ones behaviour with respect to alcohol consumption.  I think what you want is to get people being diagnosed with HIV, randomize them to enrollment in a clinic of this nature versus not.  Then follow them to see how they change their drinking behaviour.  You want to randomize at the time of HIV diagnosis, and you want to assess outcomes perhaps every month (which should be a reasonable time to expect a change, and minimize measurement errors).  This would probably be a pointless trial, that perhaps cannot be done, since current thinking is that HIV infected patients should be enrolled into some kind of chronic care program.  Albeit, it is possible to imagine that in a future where HIV treatment has been liberalized, patients could be deciding whether to enroll into a specialized HIV clinic or to seek being treated from their primary care provider for their HIV infection as for any other illness.

Attached.