MAKE this a better outcome

The PRESERVE Trial, which was recently published in the NEJM was a large study of a variety of preventive measures for contrast-induced nephropathy. It used a 2x2 factorial design to test the efficacy of NaHCO3 vs. normal saline and n-acetylcysteine vs placebo for the prevention of CIN. The trial was stopped early as there were no signals that any of the treatments were better than any other suggesting that the best treatment for CIN right now is likely the use of both saline and the smallest possible quantity of low-osmolar contrast. The overall decline in the rates of CIN over the last few years are likely more related to the change in the way that contrast is used rather than any special benefit that we were imparting using novel measures to prevent CIN.

The trial was enriched to try and increase the rate of AKI - it included patients with an eGFR between 15 and 45 (non-diabetic) increasing to 60 in diabetics. The overall mean eGFR was 50 so perhaps there were not quite enough patients with advanced disease but given that more than 5000 patients were included in the study, it is hard to really draw the conclusion that it was underpowered for subgroups. Patients with AKI were also understandably excluded and it is unclear what the risk is in this subgroup of patients.

The other thing that was really interesting about this study was the outcome used. Traditionally, studies on CIN have used AKI as the outcome. This being defined typically as some change in creatinine in either absolute or percentage terms. The current AKIN definition of stage I AKI is a 0.3mg/dl increase. This study used an increase of 0.5mg/dl. AKI of this magnitude has been shown in large studies to be associated with adverse outcomes including increased length of hospitalization and mortality but there is always a lingering question about how clinically significant it is in the long run when it tends to resolve in most patients.

Because of these concerns, there has been a recent move towards using MAKE (major adverse kidney events) as a composite outcomes in trials of kidney disease. This concept, stolen somewhat from the cardiology literature is thought to be more meaningful as it results in real, long-term harm to patients. In this study, the authors chose MAKE90 - a composite of death, need for dialysis and permament 50% increase in creatinine at 90 days as the outcome. Overall, approximately 9% of patients had AKI following contrast administration and about 4.5% had a MAKE90 event (2.5% died, 1.5% required dialysis and 1% had a permanent decline in renal function). Another thing I would take away from this study is that we should not let people tell us that CIN does not exist (which I have heard around the halls more often than I like over the last year or so).

Overall, I think this move towards MAKE as an outcome in clinical trials is a welcome one. It is a well defined outcome that demonstrates clear harm to patients. There is no reason to chuck AKI out completely - it is a perfectly good secondary outcome - but in terms of figuring out who are the patients most likely to benefit from interventions in the future, MAKE is the way to go

Immortality

A few months ago, a paper was published in the International Journal of Epidemiology that caused a sensation in it's home country - Denmark. Using registry data, and the diagnosis of non-melanomatous skin cancer as a proxy for sun exposure, the authors found that the OR for mortality in individuals who developed skin cancer compared to those who did not was 0.53. The p-value was an unfeasibly low 2x10E-308. However, when the results were stratified by age, the OR was a much more reasonable 0.97 in the sun-exposed group. This fact was conveniently forgotten when the study was reported in the media which uncritically stated that people who get more sun will live longer - something which upset the Danish cancer societies immensely.

So why was there such a disparity between the two results and how could it be possible that individuals with cancer could live so much longer (8.5 years on average) than those who did not get cancer. This month, a mea culpa editorial was published in IJE explaining their mistake along with an article discussing the entire issue. What the authors did in this case was fail to account for the immortal time bias. In this study, individuals entered the cohort when they were 40 years old. However, most people did not develop skin cancer until they were in their 60s or 70s. As a result, for the skin cancer cohort, there were approximately 20 years where they could not have died (they had to survive until they developed cancer and were "immortal" until that time). Someone who did not develop skin cancer could have died at any time during that 20 year period. To demonstrate how this works, the authors of the follow-up study, using the same dataset, randomly allocated a "lottery prize" to a proportion of individuals with a mean age of 68 who lived in Denmark over the last 20 years. Again, in this case, a person who received the prize would have had to have lived until the time that it was awarded while those who did not get the prize could die at any time. The results of the simulation study were very similar to the skin cancer study with an OR for all-cause mortality of 0.5 for the prizewinners and a similarly outrageous p-value.

This issue was first described in the 1800s when it was noticed that generals and bishops live longer than lieutenants and curates. Again, this is because one has to survive to an older age to become a bishop or a general and not because there is something inherent in these ranks that lead to an improvement in mortality.

This example is particularly egregious and the editors of IJE have to be congratulated for the way that they dealt with it. However, there are more subtle examples, one of which, highlighted in the follow-up article, appeared in JASN in 2010. This paper found that survival after transplant failure was improved by nephrectomy. However, the mean follow-up in this paper was only 2.93 years and the mean time to nephrectomy was 1.66 years. Thus, about half of the follow-up in individuals who had a nephrectomy was immortal time - they could not die during that follow-up period because they had to survive to the time of surgery. Most of the difference could be accounted for by this bias.

Similarly, a study in JASN in 2007, found that individuals enrolled in a multidisciplinary care clinic were more likely to survive than those who were not. Again, the time of the first MDC clinic was about 1 year after enrollment in the study. Individuals who entered the MDC program had a year of immortal time compared to individuals who did not enter MDC. This was pointed out in a follow-up article in KI. The authors of the original paper reanalyzed their data to account for this bias and found that MDC was still associated with improved survival although the magnitude of the effect was substantially less.

This is a fascinating issue and probably affects more cohort studies than we think. As a reviewer, I'll certainly try to look out for it in the future.

The ongoing debate about the definition of CKD in the elderly

In NDT this month, there is a nice series of articles outlining the ongoing debate about whether or not an eGFR<60 should be considered a disease, particularly in the elderly. The pro side was argued by Giuseppe Conte and the anti by Richard Glassock. Finally, there was a moderator's opinion written by Stein Hallan and Ron Gansevoort.

Dr. Glassock makes the familiar argument that age-related decline in GFR is ubiquitous and should not be considered a disease (with the associated anxiety and insurance issues that accompany such a diagnosis). This is particularly the case in elderly patients with stage 3a CKD and no albuminuria who almost never progress to ESRD and, in fact, whose eGFR declines at a rate of approximately 1ml/min/year. Labeling these patients as "CKD" leads to a huge expansion in the number of individuals diagnosed with CKD over the age of 75 in particular encompassing a significant proportion of the US population who reach this age.

In this, he is countered by both the con side and the moderator who take the position that CKD 3a is something that should not be ignored and should not be considered a part of normal aging.The most convincing argument in favor of this position is the relative risk of death from cardiovascular disease in patients with moderate reductions in eGFR relative to those with preserved renal function. It is well known that CKD is associated with an increased risk of CVD. Although the relative risk of CVD decreases as individuals age, even in elderly patients, those with CKD stage 3a are approximately twice as likely to die of CVD than those without CKD. This risk is present whether or not individuals have proteinuria. As the moderator points out, in the 1970s, high blood pressure and high cholesterol were ignored in the elderly as they were seen as being a normal part of aging despite the fact that epidemiologic data suggested that these were associated with adverse outcomes in the elderly too (although, as with CKD, the relative risk was reduced compared to younger individuals). eGFR-defined CKD is an independent risk factor for cardiovascular disease. The fact that there is an absence of specific therapies that could be used in this population to slow decline or attenuate CVD risk (beyond traditional risk factor treatment) does not mean that it should be ignored. In fact, given the high prevalence of this condition in the general population, and the number of excess CVD deaths that can be attributed to CKD, this is an area where research should be focused to determine how we can reduce risk in these patients. I'm afraid I have to go with the moderator and Dr Conte on this one.

Screening for CKD - The new ACP guidelines - Part 3

Recommendation 3: The ACP recommends that clinicians select pharmacologic therapy that includes either an angiotensin-converting enzyme inhibitor (moderate-quality evidence) or an angiotensin II-receptor blocker (high-quality evidence) in patients with hypertension and stage 1 to 3 chronic kidney disease. (Grade: strong recommendation)

This is the recommendation that I have most of a problem with. The most recent KDIGO guideline on the management of blood pressure in CKD is 85 pages long and although this degree of detail is not necessary for a guideline for general practioners, there is a substantial amount of nuance that has been missed and, in fact, I believe that this recommendation is potentially harmful.

It is clear from many RCTs going back to the 1980s that ACE/ARB therapy is indicated for the treatment of hypertension in all individuals with UACR>300mg/g. Similarly, ACE/ARB are also indicated for all diabetic patients who have a UACR>30mg/g. However, there is no clear evidence that ACE/ARB are preferred in non-diabetic patients with a UACR between 30 and 300 mg/g. The current KDIGO guidelines grade the evidence for the use of ACE/ARB in that setting as 2D (the lowest quality evidence) although there are suggestions from trials that there may be benefit.

However, for non-diabetic patients without albuminuria, there is no evidence that ACE/ARB reduce CVD or mortality relative to other antihypertensives. In fact, there is evidence that ACE/ARB are associated with more complications in non-proteinuric patients (AKI, hyperkalemia etc.) In the TRANSCEND trial the investigators studied the use of telmisartan in patients who could not tolerate ACE inhibitors. Of note, none of the patients had macroalbuminuria although all were high risk individuals. A pre-specified secondary analysis of this study examined renal outcomes and found no significant difference in the treatment group vs. placebo. However, when these patients were separated into those with and without albuminuria, there was a trend towards a benefit in those with albuminuria. In patients without albuminuria, there was an interaction for the main renal outcome (p=0.01) in the direction of harm (HR 2.35, CI 1.33-4.15). This result is not altogether surprising. In my (admittedly anecdotal) experience, the use of ACE/ARB in patients with non-proteinuric kidney disease is hazardous. These patients, usually elderly, are prone to hypotensive episodes and are exquisitely sensitive to volume depletion. the majority have vascular renal disease, even if they do not have clinically significant renal artery stenosis.

It appears that the authors of the recommendation did not take albuminuria into account when formulating this guideline. I would alter it to state that ACE/ARB should be first line therapy in patients with CKD and albuminuria but that they should be used with caution in patients with no albuminuria, particularly in the elderly and those with vascular renal disease. Score this a 0.

Recommendation 4: The ACP recommends that clinicians choose statin therapy to manage elevated low-density lipoproteinn in patients with stage 1 to 3 chronic kidney disease. (Grade: strong recommendation, moderate quality evidence)


This is a pretty uncontroversial statement. Although the benefits of statins in patients with ESRD are no clear-cut, two recent meta-analyses have clearly demonstrated that statins reduce CV mortality in patients with early stage CKD. Score 1.

Overall, I would score these guidelines 2.5/4. Reading around this has certainly highlighted to me the lack of good RCTs to guide therapies that we treat as routine and suggests many avenues for future research although it is difficult at this stage to see who would pay for these studies as they would need to be extremely large and hence, very expensive.

Screening for CKD - The new ACP guidelines - Part 2

Recommendation 2: The ACP recommends against testing for proteinuria in adults with or without diabetes who are currently taking an angiotensin-converting enzyme inhibitor or an angiotensin II-receptor blocker. (Grade: weak recommendation, low quality evidence)

This is an interesting recommendation and from a nephrologist's perspective, at first glance, it appears inappropriate but it should be remembered that these guidelines are not aimed at nephrologists but at primary care doctors and internists who are not dealing with patients who have frank nephrotic syndrome. This is similar in a way to the new guidelines for managing LDL cholesterol - there is no longer a specific target and regular monitoring of LDL is recommended only to demonstrate an appropriate response to therapy and compliance with treatment.

What is the evidence for UACR monitoring in patients with CKD. First of all, all patients with macroalbuminuria and all diabetics with microalbuminuria should unequivocally be on RAAS blockade unless there are contraindications. However, there are no trials demonstrating that targeting a specific level of proteinuria or that regularly monitoring proteinuria improves outcomes. With the recent demise of double RAAS blockade, it could be argued that once an individual is maximized on a single drug, regular checks of UACR are not going to alter therapy anyway.

That said, I do feel that there is value in rechecking UACR levels in patients on therapy. The ONTARGET Study showed very nicely that response to therapy was an excellent predictor of long term outcomes. A greater than twofold increase in albuminuria from baseline to 2 years despite therapy was associated with a 50% increase risk of mortality and a 40% increased risk of ESRD or doubling of creatinine. In contrast, a twofold decrease in UACR was associated with a 15% decrease in mortality and a 25% decrease in renal outcomes. Thus, periodic measurement of the UACR, despite its faults, provides important prognostic information.

The UACR is a surrogate marker and as a result it is suboptimal but if we learned anything from the Bardoxolone saga, it was that we should not ignore increasing albuminuria as a signal of adverse outcomes. As I said, this guideline was aimed at PCPs and it can certainly be argued that checking the UACR at every visit will not be enormously beneficial in that setting, particularly in patients with minimal albuminuria and early stage CKD. However, I don't think nephrologists will stop checking the UACR anytime soon, or stop seeing its value. However, I would agree that we do not know for certain what to do with an increasing UACR in a patient on maximal ACE/ARB therapy or what level we should be targeting. I would score this one 0.5/1 (total so far, 1.5/2)

Screening for CKD - The new ACP guidelines - Part 1

A few days ago, I was asked to present the new ACP guidelines for screening for CKD stages 1-3 to a group of non-nephrologists. These guidelines were published online last October in Annals of Internal Medicine and provoked a furious response from some nephrology groups including the ASN. The ASN's statement in particular took issue with the first recommendation and suggested that population screening of adults for CKD was justified. I'm going to present the 4 recommendations, briefly review the evidence and give a score for each recommendation based on what I believe. I know I'm sticking my neck out but I welcome any comments.

1. The ACP recommends against screening for CKD in asymptomatic adults without risk factors for CKD. (Grade: weak recommendation, low quality evidence).

In the response to this the ASN said "If detected early in its progression, kidney disease can be slowed and the transition to dialysis delayed. This evidence based fact is why regular screening and early intervention by a nephrologist is so important to stemming the epidemic of kidney disease in the US and why the ASN strongly recommends it". The problem with this response is that there is no evidence from trials that it is true. Remember that it is stages 1-3 CKD that we are talking about and that about 50% of individuals identified through screening will have stages 1-2. The risk of progression to ESRD in this population is very small. Note that the recommendation only refers to adults without risk factors. There is no suggestion that individuals with risk factors (diabetes, hypertension etc.) should not be screened.

The PREVEND study screened 41,000 adults in the Netherlands for albuminuria. After 9 years follow-up, 45 individuals required RRT. Screening only those who had risk factors (a history of hypertension, diabetes or CVD) identified 87% of those who eventually required dialysis. Of the 26,000 individuals without risk factors who were screened, only 5% had albuminuria and just 6 eventually required dialysis. Of those 6, only 2 had albuminuria at the time of screening. More recently, a cost-effectiveness study sponsored by the CDC found that the cost per QALY of screening was $155,000 for adults without risk factors compared with $21,000 for those with diabetes and $55,000 for those with hypertension when using CKD progression/ESRD as the outcome. It should be said that a subgroup analysis of the PREVEND study did find that there was marginal benefit to screening for microalbuminuria to prevent CVD with ACEi treatment. The benefit was substantially higher if only those with risk factors or individuals over the age of 60 were included. Another recent study examined the cost-effectiveness of albuminuria screening in African Americans and found that the cost-effectiveness was far higher in this population. However, they made a number of assumptions including that ACE therapy would be as effective in non-diabetics and non-hypertensives as in patients with these conditions and that ACE therapy would have the same effect on CKD progression as it does in non-African Americans.

It should be noted that the ACP is not the only group that recommends against population screening for CKD. The US Preventative Services Task Force also recommend against screening while the most recent KDIGO guidelines recommend screening for albuminuria and decreased GFR only in individuals with risk factors. Even KDIGO has an issue with the frequency of screening and recommendations range from yearly to every 3 years depending on the presence of co-morbid conditions.

Overall, after reviewing the (extremely poor) evidence, I would tend to agree with the ACP on this one. However, given the high prevalence of CKD in older populations, I would perhaps include individuals over the age of 65 in the group of those who should be screened along with patients with diabetes, hypertension and a family history of CKD. Score one for the ACP.

After writing this, I realize that I can't deal with all of the recommendations in one post so I'm going to split it up and post on the remaining recommendations over the weekend.

Hemodialysis vs. Peritoneal Dialysis

My attention was caught by the recent article in CJASN which compared the mortality of peritoneal dialysis (PD) and hemodialysis (HD) patients in the first 2 years of dialysis therapy. When comparing survival outcomes of PD and HD patients, the data we have so far is based on observational studies. A randomized controlled study has never been successfully completed because of difficulties in randomization. The only randomized study so far - the NECOSAD study (Netherlands) managed to randomize only 5% of the eligible subjects3.  

Most of the observational studies looking at survival had methodological limitations like suboptimal adjustment for modality switch over time (PD patients more likely to switch to HD), inability to account for time-varying confounding by laboratory values and inappropriate adjustment for the differential longitudinal censorship of transplantation across modalities (PD patients more likely to get a transplant). While analyzing such time-varying covariates which are simultaneously confounders as well as predictors of outcome and subsequent exposure, traditional methods like logistic or proportional hazards regression are biased and hence they pose unique analytical challenges. Hence a new statistical model – a Marginal Structural Model (MSM) which employs  inverse probability weights (IPWs) to determine the effects of these time varying covariates on the primary outcome (which was survival  in this study) was utilized  in this study. In order to adjust for the effect of each dialysis modality and censorship from transplantation, a combination of inverse probability of treatment weights (IPTWs) and inverse probability of censoring weights (IPCWs) was used. The IPTW (or IPCW) will have estimated probabilities of treatment (or censorship) using baseline covariates as the numerator and estimated probabilities of treatment (or censorship) using baseline and time-dependent covariates as the denominator. The MSM helped to derive meaningful survival data, adjusting for the above mentioned confounders

The study used information from two large databases viz. USRDS and Da Vita, providing a large cohort of almost 24000 incident dialysis patients. Separate analysis was conducted using a Kaplan–Meier survival curve, cox proportional hazards and the MSM model. A 48% greater survival for incident PD patients at 2 years was found using the MSM model. These findings were in contrast to findings in other studies in the past which showed either no difference in survival or marginal survival advantage especially in the first year for PD compared to HD5. Additionally, a comparison between the cox model and the MSM   demonstrated that the time-dependent confounders determined the difference in survival. Changes in modality during the first 2 years of dialysis affected the survival patterns over time and the reason for this trend is not completely understood at this point. This study supports greater use of PD in the treatment of ESRD patients especially in US where less than 8% of prevalent patients with ESRD are on PD.A comprehensive dialysis modality education program should be encouraged to expand the practice of PD.

See these two previous posts on the debate between PD and HD.

Posted by Bijin Thajudeen

Time for a change?

This month's issue of NDT has an interesting debate concerning whether or not clinical laboratories should start reporting CKD-EPI GFR instead of MDRD. The pro side is here while the con side is here. Basically, the argument for changing is that there is less bias in the CKD-EPI equation, it is more accurate at higher GFRs and more accurately classifies patients as stage 3 as opposed to stage 2 (in terms of overall prognosis). The counter-argument is that, although there is a slight decrease in bias associated with the use of CKD-EPI, it is not any more precise than MDRD - this is more a fault of creatinine as a test of renal function rather than a specific problem with the equations. It should also be mentioned that the CKD-EPI equation is not necessarily better in all circumstances - as documented by Leo in this post about renal transplant recipients.

To (perhaps) settle the argument on one side, the moderator of the debate wrote a commentary and came down on the side of changing to the CKD-EPI equation. The argument is that, even if the improvement is slight, we, as a nephrology community, should not settle for something that is clearly inferior in most circumstances. MDRD was developed in a population of patients with CKD and therefore does not accurately reflect GFR in healthy populations. For this reason, in the research community, there has been a move towards more use of CKD-EPI in the recent past as it is more appropriate for epidemiologic research. The switch to CKD-EPI would not require the use of any new analytes - a simple change in coding in the computers reporting results. In fact, a number of organizations have already switched.

Two other things to mention. Neither equation has been properly validated in Asian populations and this needs to be remedied. Secondly, the role for cystatin C-based or combination equations is still uncertain. Cystatin C is a better predictor of outcomes than creatinine but there are many non-GFR determinants of cystatin C that are likely biasing this and are not related to renal function. Also, the cystatin C test is expensive and has not been fully standardized. There may be a place for the combination equation in patients with borderline GFRs (45-60) in whom the diagnosis of CKD is uncertain.

Falsification Analysis

Interesting paper this month in JAMA about post-marketing studies of adverse drug effects. Randomized controlled trials are obviously the gold standard for the detection of common adverse events related to treatment. The problem is that, if an adverse event is rare, it is unlikely to be detected by a normal RCT. As a result, there has been a move recently towards conducting post-marketing studies of commonly used drugs to identify rare adverse effects. One such effect mentioned in the study is the association between bisphosphonate use and atypical femoral fractures.

The other commonly cited example recently was the association between PPI use and community acquired pneumonia that has been noted in multiple studies. The putative mechanism is that it is due to a reduction in gastric pH. The problem is the question of residual confounding - is there an alternative reason that these patients have more pneumonia. Are these patients simply sicker overall? Are PCPs who prescribe PPIs more likely to diagnose pneumonia? Just because there is a plausible mechanism doesn't make it true.

One potential solution is to perform a falsification analysis. Once you have determined the primary outcome of the study (in this case pneumonia) with a plausible outcome, you then perform a series of prespecified analyses with other non-plausible outcomes. If all of the outcomes are associated with the use of PPIs, it suggests that the association is more likely related to residual confounding rather than a real effect.

In the study referred to in the JAMA article, the authors, working from registry data, not only found an association between PPI use and pneumonia but also with osteoarthritis, urinary tract infections, rheumatoid arthritis, chest pain, DVTs and skin infections. Thus, they suggested that the association with pneumonia was more likely to be confounded because of the lack of a plausible relationship with these other adverse events. One criticism I would have is that I could think of perfectly reasonable hypotheses for why PPI use could be associated with OA and RA (use of NSAIDs) and chest pain (GERD). Another important point is that if this is not done properly (prespecified adverse events) you could find an association between the use of a drug an some adverse event if you tested enough and it could be used to wrongly refute the association between a drug and a problem.

Still, the whole article is a fascinating insight into the problems with post-marketing studies of drugs in the wider population.

Miracle Drug?

The above figure compares long term survival in a subgroup of a trial that was published in Circulation in 1980. This was a randomized controlled trial of just over 1000 patients with known cardiovascular disease who were treated with medical therapy alone. The patients were randomized to two treatment groups and were followed for 5 years. In the primary analysis, there was no statistically significant difference in survival between the two groups. However, a subgroup analysis that compared only patients with 3-vessel disease and LV dysfunction at baseline (~200 patients in each group) found that the outcomes were significantly better in group B (p=0.025).

So what was this treatment that was so successful in reducing mortality in group B? There was no treatment. The patients were randomized to the two groups and then simply followed with usual therapy. This study was designed to show the danger of subgroup analyses and why they should be taken with a grain of salt. When the authors looked deeper into the data, it became apparent that the patients in group B were not as sick as those in group A and that the survival difference was non-significant in a multivariable analysis. However, when they further stratified the patients by only including those with no history of congestive heart failure, the difference between the groups became more significant and remained significant in the multivariable analysis (p=0.01).

We are often confronted by negative clinical trials in nephrology and other disciplines and there is a natural tendency to try and find something useful when these trials are completed. Like any multiple comparison, if you do enough subgroup analyses, you will eventually find one that is significant. Any good statistician will tell you that this needs to be accounted for in the final analysis but this is not necessarily always done. Think about this trial when you are reading about the wonderful effects of a treatment that was negative for most but efficacious for a small group of patients with very specific attributes.