Hospitalist JC 11/14/11

Dr. Nang: Apixiban versus Warfarin in Patients with Atrial Fibrillation
Click here to listen to a recording of Dr. Nang's presentation.

Dr. Nang presented a large trial of warfarin vs. apixaban which was designed to prove the non-inferiority of apixaban for preventing stroke in atrial fibrillation.  The primary efficacy outcome was a compound of stroke and systemic embolism, and the primary safety outcome was bleeding.  They also analyzed their results for subtypes of stroke (ischemic vs. hemorrhagic) and bleeding (e.g. gastroinestinal, intracranial, etc.).  The study was large, multi-centered, and used a randomized, double dummy design.  The baseline demographic data they reported indicated highly successful randomization, and analysis was by intention to treat.

Their results showed that in their sample, apixiban was non-inferior to warfarin both in terms of reducing the risk of the primary outcome (HR 0.79 (0.66-0.95), P = 0.01) and in reducing the rate of major bleeding (HR 0.69 (0.6-0.8), P= <0.001).  The reduced incidence of stroke appeared to accrue primarily from a reduction in hemorrhagic stroke relative to warfarin (HR 0.42 (0.30-0.58) P = <0.001).

Some important points were raised during the discussion.  Dr. Flattery and Dr. Feeney both pointed out that, while the trial design and execution appear fairly impeccable based on the article, one should not ignore the extremely close involvement of the manufacturers.  Primary analysis were performed at Bristol-Myers-Squibb, its representatives had a say in trial design, participated in the study design, and the investigators had an enormous variety of relations to an inordinate number of pharmaceutical companies, including BMS and Pfizer.  Dr. Rose pointed out some sleight-of-hand at the end of the article: the trial was designed to prove non-inferiority; however, the investigators report that "apixiban was superior to warfarin in preventing stroke or systemic embolism, caused less bleeding, and resulted in lower mortality."  All of these conclusions would require another study powered for superiority to demonstrate.

Fig 1. Hazard Ratios. Prevalence is on the Y axis, time on the X.

The results were reported in hazard ratios, which (as a reminder) are similar to relative risk but are derived slightly differently.  In survival analysis (which is used to analyze many things other than survival,) people frequently use Kaplan-Meier curves, which plot the incidence of an event over time.  So long as the incidences of the event being studied in the treatment and control groups remain proportional, a ratio of the two can be taken at any point along the curve and should yield the same number, which is the hazard ratio (see Fig. 1).  Thus, a hazard ratio of 2.0 means that the hazard (i.e. the event being studied) is twice as likely to occur at any given point in time in the experimental group than the control group.

Dr. Jafari: Association of Hospitalist Care with Medical Utilization After Discharge: Evidence of Cost Shift from a Cohort Study.

Click here to listen to a recording of Dr. Jafari's presentation
 
Dr. Jafari presented a retrospective cohort study which looked at length of stay, hospital charges, and post-discharge healthcare usage among Medicare patients who were cared for by hospitalists and those who were cared for by their primary care providers (PCP) while in the hospital.

The statistical analysis, which was rather baroque, appeared to show that the patients cared for by hospitalists stayed in the hospital for around a day less, that their hospitalization was cheaper by about $282.00, and that their post-discharge healthcare costs were higher by about $332.00 compared to patients whose PCP cared for them in the hospital.  Moreover, hospitalist care was associated with a marginal risk of re-admission (OR 1.08), ED visits (OR 1.18) and a reduced chance of discharge home (OR 0.82). 

Dr Green-Yeh noted that while these results may have some validity, time is not moving backwards and PCPs are not coming back into the hospital.  She suggested that this study is more useful as a foil for policy discussion than an argument for returning to the "traditional" model of hospital practice.  Dr. Remler saw a number of problems with the study, one of the foremost being that most of the included hospitals were teaching hospitals; this, he argued, disorts the results significantly, since the hospitalist movement began in community hospitals and has primarily flourished there.

Dr. Rose and Dr. Singh both pointed out that there was no analysis by severity of illness, which would seem to be a critical feature to consider given that general internists increasingly defer management of the sickest patients to hospitalists.  Dr. Rose also pointed out that the present Medicare system reimburses hospitalization at a set rate based on DRG, whereas Medicare outpatient visits are reimbursed on a fee-for-service basis, creating an obvious incentive to shorten hospitalization at the expense of outpatient service utilization.

Dr. Flattery and Dr. Sackrin commented that another limitation of this study is that it doesn't account for the lost daytime productivity of a PCP working in a hospital.  Dr. Feeney concluded by emphasizing that what this study really demonstrates is how important it is, when working in an inpatient environment, to strive for continuity of care with patients' outpatient doctors.


Dr. Ha: Venous Thromboembolism Prophylaxis in Hospitalized Patients: A Clinical Practice Guideline From the American College of Physicians

Click here to watch a recording of Dr. Ha's presentation - unfortunately, there's no audio.
 
Dr. Ha presented both a new guideline from the ACP on VTE prophylaxis, and the background evidence review which supports it.  The new guideline (below) is based on a systematic review of the literature on heparin (unfractionated and low-molecular-weight) for the prophylaxis of VTE in medical patients and patients suffering from acute stroke.

 

The guideline contradicts conventional wisdom and many hospital's internal performance standards in questioning the utility and safety of generalized VTE prophylaxis with heparin products.  However, the background paper is, as Dr. Feeney noted, even more pessimistic than the guideline.  The authors conclude:

When considering medical patients and those with stroke together, low dose heparin prophylaxis may have reduced PE and increased risk for bleeding and major bleeding events and had no statistically significant effect on mortality.  We interpret these findings as indicative of little or no net benefit.

 There were some other interesting features of the guideline and review.  First, the authors make an implicit judgment about the cost-efficacy of low-molecular weight heparin as opposed to unfractionated.  While they did observe an increased incidence of heparin-induced thrombocytopenia among patients given unfractionated heparin (which is generally given as the main reason to use low-molecular weight heparin), the incidence in both groups was so low that they suggested the decision as to which product to use should be made on the basis of "ease of use, adverse effect profile, and cost".  Second, they found insufficient evidence to support the use of pneumatic compression devices to prevent DVT.  Finally, the absolute effect sizes derived from their review were infinitessimal.  The estimated that the number-needed-to-treat to prevent one pulmonary embolus in medical and stroke patietns considered ogether was around 333, and the number needed to cause a major bleed was 250.  This suggests that for the vast, vast majority of medical patients, heparin products do absolutely nothing.

Dr. Green-Yeh commented that what is clearly needed, and unfortunately does not yet exist, is a validated tool for establishing VTE risk in medical inpatients based on risk factors.  Some patients must benefit much more than others - but how the "assessment of the risk of VTE" recommended by the ACP is to be carried out is not at all clear.  She also pointed out that this guideline ought to have major implications for pay-for-performance measures involving VTE prophylaxis, which presently are based on the nebulous and apparently wrong sense that heparin prophylaxis should be standard of care unless contra-indicated.

ICU JC 10/13/11

Therapeutic hypothermia in action

Dr. Xuan presented a retrospective study of therapeutic hypothermia (TH) after cardiac arrest due to PEA and asystole.

It is well-established that therapeutic hypothermia following out-of-hospital arrest due to shockable rhythms is associated with improved neurological outcome in survivors, and current AHA guidelines recommend cooling for twenty-four hours in any unconscious survivor of out-of-hospital VF arrest.  However, it is not clear whether this benefit extends to inpatients, or to patients presenting with non-shockable rhythms.

This trial assessed data prospectively collected at Hartford Hospital in Connecticut to determine whether the introduction of a cooling protocol for patients resuscitated from non-shockable rhythms changed outcomes for those patients.  The trial group was compared to a group of historical controls, and the investigators claimed to have found a statistically significant difference in neurological outcome, which is consistent with the results of other observational studies and meta-analyses.  However, the study had a number of limitations which came out in the discussion which followed Dr. Brah's presentation.

Dr. Bhuket emphasized how important it is to carefully review the baseline characteristics of the treatment and control groups in any type of trial ("Always look at Table 1").  He pointed out that in this study, the two groups differed markedly in age, presenting rhythm, whether the arrest was witnessed, and other characteristics presumably important to the outcomes observed.  He also drew attention to the fact that the authors are employed to promote the device used to induce hypothermia in the study.

Dr. Subramanian noted that, given that medical care is always changing, the use of "historical controls" is always perilous.  She wondered whether it's genuinely plausible that over the six-year period during which data were collected, nothing changed in post-cardiac arrest care at Hartford hospital besides the use of therapeutic hypothermia, and whether this might further confound the results. 

The expert consensus was that there may be reasons to use therapeutic hypothermia after resuscitation from a non-shockable rhythm, but that they should not be drawn from a study with as many methodological limitations as this one.

It's worth noting that there are two typos in this article in its present form:

1. The authors say that they calculated a NNT from the "absolute risk ratio."  This is an accidental compound of "absolute risk reduction," which is what you calculate the NNT from, and "relative risk ratio," which has nothing to do with absolute risk changes.  When I contacted Dr. Lundbye, he confirmed that this was a typographical error.
2. The NNT to achieve "one favorable neurological outcome" is given as 5.  However, if you calculate it from the data in presented in the paper, it's actually 6.  The difference is trivial in this instance, but reminds us to check others' work rather than accepting it without question.

Curare (source of the first NMJ blockers)

Dr. Indulkar presented a randomized, controlled trial of cisatracurium in early ARDS which tested the hypothesis that early paralysis might confer improved 90-day mortality.

Patients randomized to the treatment arm received cisatracurium besylate for 48 hours.  In an effort towards blinding, the investigators prohibited the use of peripheral nerve stimulators to objectively confirm paralysis, and patients randomized to the control group received a placebo infusion.  The authors managed to demonstrate a statistically significant difference only in "adjusted" 90-day mortality (although the difference in crude mortality was nearly significant with a p value of 0.08), and in some of their secondary end points.  The discussion focused on the validity of the study's results, and some important points came up.

Dr. Schub and Dr. Sackrin agreed that it would be very premature to implement early paralyis in ARDS on the basis of this study for several reasons.  First, Dr. Sackrin noted, the test used to establish the incidence of ICU-acquired paresis was crude and the investigators may therefore have underestimated the harm associated with their treatment.  He also noted that it would be hard to generalize the results to our patients, since we use vecuronium almost exclusively in patients with normal renal function. 

Dr. Feeney, who had pulled the article's enormous appendix and read through its long tables of vent-setting data, pointed out something very interesting: the proposed mechanism of increased survival in the trial was improved patient/ventilator synchrony.  However, there are no differences in the vent data between the two group suggesting a higher prevalence of dysynchrony in the control group - so that mechanism isn't supported by their actual data.  He also thought generalization to our patients would be problematic, because the data in the appendix showed oxygen saturations much higher than those we typically aim for in ARDS and a general reliance on a high FiO2, low PEEP ventilation strategy, which is also significantly different from our practice.

Dr. Subramanian drew attention to three important problems with the article:

1. The Kaplan-Meier survival curve presented in Figure 2 shows a divergence in probability of survival at 12 days.  However, the drug was given only in the first 48 hours.  This makes a neat causal relation difficult to imagine, and should make one suspect the presence of unmeasured confounders.
2. Cisatracurium is associated with tachyphylaxis, and because objective measurements of paralysis were not allowed, it's impossible to know who was actually paralyzed.
3. The assumptions about mortality used to power the study turned out to be incorrect, so the study itself was ultimately underpowered to demonstrate its primary outcomes.
   

Child in a Ugandan hospital

Dr. Brah presented a trial which compared bolus fluid resuscitation to no specific fluid resuscitation therapy in febrile, hypotensive children presenting to district hospitals in three East African countries.

This was a prospective, multi-center, open-label trial comparing fluid resuscitation with boluses of either normal saline or 5% albumin.  Children with severe febrile illness and impaired perfusion were included; children were excluded if they had severe malnutrition, gastroenteritis, non-infectious causes of shock, or contraindications to volume-expansion.  All participating children received antibiotics, antipyretics, antimalarials and other standard therapies for severe infection according to national guidelines.

Why, you may be asking yourself, was this study, which looked at rural African children, presented at a meeting attended exclusively by internists practicing in an American city?  Because of its alarming and unexpected results.

48-hour mortality in the saline-bolus group was 10.5%, in the albumin-bolus group it was 10.5%, and in the control group it was 7.3%, suggesting an absolute risk increase of about 3% associated with fluid resuscitation.  They also observed a risk increase of 4% at 4 weeks for death, neurologic sequelae, or both in the two resuscitation groups.  Subgroup analysis did not identify any group for which fluid resuscitaion was beneficial.  Interestingly, most deaths were not obviously associated with the recognized ill-effects of over-resuscitation in children, e.g. pulmonary edema and elevated ICP.

This article generated a very lively discussion. 

Dr. Rose and Dr. Schub were deeply concerned about the ethics of the study.  Dr. Rose expressed doubt that legitimate informed consent could have really been obtained under the conditions which prevailed at the study centers, while Dr. Schub saw serious problems testing a therapy with predictable adverse effects (such as pulmonary edema) in the absence of means for dealing with them (such as positive-pressure ventilation).

Dr.s Feeney, Subramanian, Sackrin, and Fried agreed that the study was primarily interesting as a hypothesis-generator, and because it calls into question ideas which have become axiomatic in the treatment of sepsis.  Dr. Feeney pointed out that, a few decades ago, a similar orthodoxy prevailed about the beneficial effects of blood transfusion - an orthodoxy which has been completely overturned by an increasingly robust body of evidence.  He quoted one of Dr. Schub's favorite aphorisms, which states that "the half-life of medical truth is about three years." "Why," he asked, "does God make you anemic?  Why does God make you hypotensive?"
While declining to add to Dr. Feeney's theological speculations, Dr. Sackrin called the study's results "humbling."  Finally, Dr. Subramanian pointed out that one plausible mechanism for the increase in observed mortality might be rapid hemodilution, since the excess mortality was mainly observed in children presenting with a hemoglobin level less than 5 grams per deciliter.

Hematology-Oncology 9/8/2011

Dr. Shi: Radical Prostatectomy versus Watchful Waiting in Early Prostate Cancer
Click the title to view a recording of the presentation.

Dr. Shi presented a very recent paper from the Scandinavian Prostate Cancer Study Group documenting the results of a trial which randomized men with prostate cancer to surgery or watchful waiting.  These results mark a median of 12.8 years of follow-up (range: 3 weeks to 20.2 years).  The investigators looked at a fairly specific group: these were men under 75 with at least a ten-year life expectancy who had localized disease diagnosed by biopsy with a PSA <50 ng/ml and a negative bone scan.  The original N was 695, of whom just over half had died by 2009, and the primary endpoints were all-cause mortality, disease-specific mortality and distant metastases.  For the most part, their tumors were diagnosed by symptoms, not population-level screening.

The authors report an absolute reduction in the risk of death from any cause of 6.6 percentage points (95% CI -1.3 to 14.5), which corresponds to a number needed to treat (NNT) of 15.  The absolute risk reduction and NNT for death from prostate cancer were similar, as you would expect.  The ARR for distant metastases was 11.7 points (95% CI 4.8-18.6) corresponding to a NNT of 8.5.   

In their subgroup analysis, it appeared that all of this benefit accrued to men under 65 (there were no significant differences in any of the three endpoints for men older than 65).  They report an absolute risk reduction for disease specific mortality of 9.4 percentage points in men under 65, although their confidence interval can't exclude a reduction as small as 0.2 points or as large as 18.6 points.

One of the most important points of the discussion, and of Dr. Shi's summary, was that this is not at all about screening for prostate cancer.  As above, these men were largely diagnosed because they presented with symptoms and many of them had palpable tumors.  So as general internists, this study gives us some guidance about what we can recommend to younger men who, for whatever reason, have received a diagnosis of early prostate cancer, but it doesn't take us beyond the USPSTF's current recommendation regarding screening:

"for men younger than age 75 years, the benefits of screening for prostate cancer are uncertain and the balance of benefits and harms cannot be determined."

Another important theme of the discussion was the low emphasis on harms associated with radical prostatectomy in this article.  The procedure has very high rate of adverse effects, particularly impotence and incontinence.  While the authors reported the 1-year cumulative incidence in the radical prostatectomy group (32% for incontinence, 58% for impotence,) they didn't give a level of detail commensurate to the exploration of benefits, which makes it hard to weigh the risks and benefits even for patients very much like those in the study.


Dr. Kim Suh: A Novel Test for Colon Cancer
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Slobbery bedside manner...

Dr. Kim Suh presented a very euphemistically entitled study from Kyushu University in Japan.  The authors tested the ability of a very highly trained black labrador retriever to detect colon cancer based on breath samples and watery stool samples.  The dog's name is Marine, and she is a fixture at the oddly but accurately named St. Sugar Cancer Sniffing Dog Training Center in Chiba, Japan.  Marine  was originally trained for water rescue, but switched careers and has been learning to detect various human malignancies since 2005.


The authors collected stool and breath samples from people with known colorectal cancer and from healthy volunteers.  All subjects underwent colonoscopy with or without biopsy as indicated, which was considered to be the gold standard against which the dog's performance was judged.  Testing was conducted between November and June, because apparently the dog has trouble concentrating in hot weather. Each test consisted of four samples from individuals without cancer and one who did have cancer.  The placement of the samples in the test room was dictated by a random number table, and their identity was blinded to the dog, the handler and the lab assistants.  However, the accuracy of the dog's identification was rapidly communicated to the handler after it made its final choice so that it could be appropriately rewarded (with a tennis ball).

Future member of Tumor Board?

The dog's results were compared with the final diagnoses at colonoscopy and with conventional FOBT testing.  With respect to colonoscopy, positive identification by the dog had a sensitivity and specificity of 0.91 and 0.99 for breath samples and 0.97 and 0.99 for stool samples.  Interestingly, there was very little correlation with FOBT, demonstrating that whatever the dog is smelling, it's not a human blood product.

Following on from the first article, it seems like the obvious question is whether the Scandinavian Prostate Cancer Study Group can train a dog to tell the difference between indolent and aggressive prostate cancer.  Then the dog could tell the surgeon who is likely to enjoy a longterm survival benefit from radical prostatectomy.  Cost-effectivness would depend on the dog's number-needed-to-smell.

Joking aside, an important thing to note about studies like this is that you can't calculate positive or negative predictive values from the data they use to give sensitivity and specificity unless the prevalence in the study population mirrors the prevalence in your own population.  This is because the likelihood of a false positive depends on the prevalence of the disease; if everybody has it, there can be no false positives, and if nobody has it there can be no true positives.  In the case of this study, the incidence of colorectal cancer in the "population" was one out of every five samples, or 20% - clearly much higher than it would be in a normal screening population - so you can't generalize a PPV calculated from this study to the real world.  This is a much commoner mistake than it seems like it should be, and is worth looking out for.


Dr. Tuason: Erythropoietin Stimulating Agents for Treatment of Anemia in Chronic Kidney Disease
Click the title to view a recording of the presentation.
 Dr. Tuason presented an article reviewing the use of recombinant human erythropoietin (rHU EPO) in the management of anemia caused by chronic kidney disease (CKD).  

The use of erythropoietin stimulating agents (ESAs) such as darbepoetin alfa, epoetin alfa and epoetin beta to boost hemoglobin levels in CKD has a controversial history.  One of the main putative benefits was historically thought to be a reduction in the incidence of serious cardiovascular events related to left ventricular hypertrophy and heart failure, for which anemia is a risk factor.  Some investigators have also claimed beneficial effects of higher hemoglobin levels on various indices of quality of life, restless legs syndrome, and bleeding time.

The authors review three recent, large trials all of which were designed to assess the optimal hemoglobin level in patients with stage III-V CKD by randomizing patients to target-based therapy with ESAs.  

The CREATE trial (2006, N=603) randomized patients to a target hemoglobin of either 13-15 g/dl or 10.5-11.5 mg/dl.  The primary endpoint was a composite of cardiovascular events.  Most patients in both group received some therapy with epoietin beta, although as you might expect more patients were treated in the higher hemoglobin target group.  There was no difference in the primary endpoints between the two groups.

The CHOIR trial (also 2006, N=1432) randomized patients to a hemoglobin target of 11.3 g/dl or 13.5 g/dl, and was terminated early by its data and safety monitoring board when a higher incidence of serious cardiovascular events including deaths, MIs, strokes and hospitalizations for CHF were observed in the higher hemoglobin group. 

The TREAT trial (2009, N=4000) randomized patients to a hemoglobin goal of 13 g/dl, or a goal of >9 g/dl with darbepoietin rescue therapy for those who fell below this level.  Again, a primary end point was a composite of cardiovascular event, and once again there was no difference.  However, there was a significantly higher incidence of ischemic stroke with a number needed to harm of about 40.

So, we have three very large, well-designed trials, none of which show any benefit to targeting higher hemoglobins and two of which show clear evidence of increases in the kind of event this drug was initially hypothesized to decrease.  However, somewhat bizarrely, the authors of this review concluded that we should "avoid the knee-jerk response of underutilization of these drugs."  They cite putative benefits in ""the need for transfusions, quality of life and exercise tolerance, [regression of] LVH" and a hypothetical reduction in the progression of chronic allograft nephropathy in transplant patients.  

This conclusion deserves a little dissection.  While it is possible that ESAs are beneficial in "reducing the need for transfusions," the need for transfusions itself is defined by hemoglobin targets which, as we have seen, are not clear.  The argument about regression of LVH is equally strange, in that the whole point of treating LVH is to prevent hypertensive cardiomyopathy and associated cardiovascular events - exactly the kind of events that ESAs clearly increased the incidence of in both the CHOIR and TREAT trials.  Allograft nephropathy is, of course, a totally different condition then the anemia of chronic renal disease, and even the authors admit that there's actually not really any published data on this anyway.  

But it's their argument about "the wealth of data accumulated in the 1980s and 1990s showing improved quality of life scores and increased vitality" which deserves special attention.  In support of this claim they cite 

• A study of Arousing Periodic Limb Movements with an N of 10, no control group and a 30% drop out rate,
• An unblinded, placeboless trial of ESAs influence on subjective assessments of quality of life,
• A trial of erythropoietin to correct hemoglobin to the normal range which showed increased energy levels.  This is, of course, exactly the range of correction which the TREAT, CHOIR and CREATE trials strongly suggest is dangerous, and finally,
• A study which they say shows "improvements in exercise training" with recombinant erythropoietin, but which as far as I can tell actually shows improvements similar to exercise training.

This, Dr. Yee pointed out, is a problem with reviews as a genre; they're put together by individuals who usually have strong views on the subject under discussion which may distort their analysis.  Dr. Irwin said that further research is clearly needed to define optimal hemoglobin levels, but that in his experience ESAs can improve quality of life and that there are cases where this benefit may outweigh the risks.  He also stressed that, in such cases, the optimal hemoglobin is the one that makes the patient feel better and discouraged the inflexible use of targets.  Finally, Dr. Yee gave an interesting oncological perspective on ESAs.  Many solid tumors over-express erythropoietin receptors, and so giving ESAs to patients with active cancer can accelerate tumor progression.

To summarize, the take-home points from Dr. Tuason's presentation, were essentially that 

1. Current optimal hemoglobin levels in CKD patients are not established, 
2. The use of ESAs to raise hemoglobin to the targets used in these trials is not beneficial and probably harmful, and
3. That one has to be cautious, when reading a review article, to try to understand how the reviewer's professional opinion may distort the conclusions they draw from the evidence.