Stats #32b: Statistical Evidence. Apples or oranges? Observational studies.

Stats #32b: Statistical Evidence: Apples or Oranges? Observational studies.

Content: This one hour training class will give you a general introduction in how to interpret research publications that are based on observational studies. There are four major types of observational studies: cohort studies, case-control studies, cross-sectional studies, and historical controls studies. There are advantages and disadvantages to each of these types of studies. In this presentation, you will apply these skills to actual published research.

Objectives: In this class, you will learn how to:

contrast the selection process in a cohort design with a case-control design;
describe the limitations of a case-control design for evaluating a diagnostic test; and
appraise the extent of temporal bias in the historical-controls design.

Teaching strategies: Didactic lectures and small group exercises.

IRB Education Credits: This class qualifies for 1 IRB Education Credit (IRBEC).

Notes: This class is an abbreviated version of Stats #32 with a focus on the strengths and weaknesses of randomized studies. The talk requires no mathematical background and uses no formulas.

Web pages included in this handout:

Abstract
Where can you find this handout?
Why don't I use PowerPoint?
Apples or oranges. How do you insure a fair comparison?
Apples or oranges. Observational studies.
Practice exercises

Where can you find this handout?

This handout and the handouts that I use for all of my seminars and training classes are a compilation of individual web pages at www.childrensmercy.org/stats. I use the "Include Page" feature of Microsoft FrontPage to combine these into a single page. You can always find the most recent version of this compilation by going to the web address listed at the bottom of this page. Links for the handouts for other seminars and classes appear at www.childrensmercy.org/stats/training.asp.

Why don't I use PowerPoint?

I stopped using PowerPoint for my presentations in the mid 1990's. This was based on Edward Tufte's advice that presenting information in a paper handout is more effective than presenting the information on a projected screen. I found this to be excellent guidance. I enjoy talking when I don't have to wrestle with a laptop computer. I look at my audience more and interact with them better. I elaborate on this in greater detail at www.childrensmercy.org/stats/weblog2004/powerpoint.asp.

Apples or Oranges? How do you ensure a fair comparison?

This material is an excerpt from Chapter 1 of my book, Statistical Evidence in Medical Trials, with some minor adaptations and updates.

Introduction

Almost all research involves comparison. Do women who take Tamoxifen have a lower rate of breast cancer recurrence than women who take a placebo? Do left-handed people die at an earlier age than right-handed people? Are men with severe vertex balding more likely to develop heart disease than men with no balding?

In each of these situations, you are making a comparison between a control group and a treatment/exposure group. I will use the terms treatment and exposure interchangably throughout this book, though I will reserve treatment for those conditions which represent an effort to produce a beneficial result and exposure to represent a condition that is, potentially harmful. You would call drinking water from a natural spring a treatment, but drinking water from a contaminated well an exposure. The distinction between treatment and exposure is not that critical though, and when I discuss a generic ‘treatment’ in this book, feel free to substitute the word ‘‘exposure’’ and vice versa.

When you make such a comparison between a treatment group and a control group, you want a fair comparison. You want the control group to be identical to the treatment group in all respects, except for the treatment in question. You want an apples-to-apples comparison.

Covariate imbalance

Sometimes, however, you get an unfair comparison, an apples-to-oranges comparison. The control group differs on some important characteristics that might influence the outcome measure. This is known as covariate imbalance. Covariate imbalance is not an insurmountable problem, but it does make a study less authoritative.

Women who take oral contraceptives appear to have a higher risk of cervical cancer. But covariate imbalance might be producing an artificial rise in cancer rates for this group. Women who take oral contraceptives behave, as a group, differently than other women. For example, women who take oral contraceptives have a larger number of pap smears. This is probably because these women visit their doctors more regularly in order to get their prescriptions refilled and therefore have more opportunities to be offered a pap smear. This difference could lead to an increase in the number of detected cancer cases. Perhaps the other women have just as much cancer, but it is more likely to remain undetected.

The possibility that oral contraceptives causes an increase in the risk of cervical cancer is quite complex; a good summary of all the issues involved is available at: www.jhuccp.org/pr/a9/a9chap5.shtml.

There are many other variables that influence the development of cervical cancer: age of first intercourse, number of sexual partners, use of condoms, and smoking habits. If women who take oral contraceptives differ in any of these lifestyle factors, then that might also produce a difference in cervical cancer rates.

Case study: Vitamin C and cancer

Paul Rosenbaum, in the first chapter of his book, Observational Studies, gives a fascinating example of an apples-to-oranges comparison. Ewan Cameron and Linus Pauling published an observational study of Vitamin C as a treatment for advanced cancer (Cameron 1976). For each patient, ten matched controls were selected with the same age, gender, cancer site, and histological tumor type. Patients receiving vitamin C survived four times longer than the controls (p < 0.0001).

Cameron and Pauling minimize the lack of randomization:

Even though no formal process of randomization was carried out in the selection of our two groups, we believe that they come close to representing random subpopulations of the population of terminal cancer patients in the Vale of Leven Hospital.

Ten years later, the Mayo Clinic (Moertel, et al. 1985) conducted a randomized experiment which showed no statistically significant effect of vitamin C. Why did the Cameron and Pauling study differ from the Mayo study?

The first limitation of the Cameron and Pauling study was that all of their patients received vitamin C and followed prospectively. The control group represented a retrospective chart review. You should be cautious about any comparison of prospective data to retrospective data.

But there was a more important issue. The treatment group represented patients newly diagnosed with terminal cancer. The control group was selected from death certificate records. So this was clearly an apples-to-oranges comparison because the initial prognosis was worse in the control group than in the treatment group. As Rosenbaum says so well:

one can say with total confidence, without reservation or caveat, that the prognosis of the patient who is already dead is not good (p. 4).

The prognosis of a patient with a diagnosis of terminal cancer is also not good, but at least a few of these patients will be misdiagnosed. The ones in the control group, the ones that entered the study clutching their death certificates, had no misdiagnosis.

What steps can you take to ensure a fair (apples to apples) comparison?

When the treatment group is apples and the control group is oranges, you can't make a fair comparison. To ensure that the researchers made an apples to apples comparison, ask the following questions:

Did the authors use randomization? In some studies, the researchers control who gets the new therapy and who gets the standard (control) therapy. When the researchers have this level of control, they almost always will randomize the choice. This type of study, a randomized study, is a very effective and very simple way to prevent covariate imbalance.

If randomization was not done, how were the patients selected? Several alternative approaches are available when the researchers have control of treatment assignment, but minimization is the only credible alternative. When researchers do not have control over treatment assignments, you have an observational study. The three major observational studies, cohort designs, case-control designs, and historical controls, all have weaknesses, but may represent the best available approach that is practical and ethical.

Did the authors use matching to prevent covariate imbalance? Matching is a method for selecting subjects that ensures a similar set of patients for the control group. A crossover design represents the ideal form of matching because each subject serves as his or her own control. Stratification ensures that broad demographic groups are equally represented in the treatment and control group.

Did the authors use statistical adjustments to control for covariate imbalance? Covariate adjustment uses statistical methods to try to correct for any existing imbalance. This methods work well, but only on variables that can be measured easily and accurately.

This webpage was written by Steve Simon on (date unknown), edited by Steve Simon, and was last modified on 2008-07-08. Send feedback to ssimon at cmh dot edu or click on the email link at the top of the page. Category: Statistical evidence

Apples or oranges. Observational studies.

This material is an excerpt from Chapter 1 of my book, Statistical Evidence in Medical Trials, with some minor adaptations and updates.

1.4 Nonrandomized studies

There are many situations where randomization is not ethical, practical, or possible. Sometimes, researchers could not in good conscience assign a dangerous exposure randomly to half of their patients.

Sometimes researchers do not have the resources to properly randomize patients. Sometimes patients and/or their physicians will select which therapy they receive. Sometimes the treatment or exposure variable represents a group that existed before the start of the research.

In these situations where randomization is not possible, you are looking at an observational study. There are four major flavors for observational studies: cohort studies, case control studies, cross-sectional studies, and historical controls studies.

1.4.1 The cohort study

In a cohort study, a group of patients has a certain exposure or condition. They are compared to a group of patients without that exposure or condition. Does the exposed cohort differ from the unexposed cohort on an outcome of interest?

Example: In a study of suicide among Swedishmen in the Swedish military service conscription register (Gunnell 2005), 987,308 men registered between 1968 and 1994 were divided into nine groups on the basis of four intelligence tests. These men were also linked to a Swedish cause of death register which identified a total of 2,811 suicides among these men. For each of the four intelligence tests, men scoring lower tended to have a higher rate of suicide.

Example: In a study of psychotic symptoms in young people (Henquet 2005), a sample of young adults aged 14–24 years were divided into a group of 320 with admitted use of cannabis and a group of 2,117 did not admit to cannabis use. Both groups were followed four years later for psychotic symptoms.

Cohort studies are intuitively appealing and selection of a control group is usually not too difficult. You have to be very wary of covariate imbalance, but other observational designs are likely to have even more problems. Do not worry about every possible covariate imbalance. You should look for large imbalances, especially for covariates which are closely related to the outcome variable.

When you are studying a very rare outcome, the sample size may have to be extremely large. As a rough rule of thumb, you need to observe 25–50 outcomes in each group in order to have a reasonable level of precision. So when a condition occurs only once in every thousand patients, a cohort study would require tens of thousands of patients.

You want to avoid ‘leaky groups’ in a cohort design. If the exposure group includes some unexposed patients and the control group includes some exposed patients, then any effect you are trying to detect will be diluted. Be especially aware of situations where one group is more leaky than the other.

For example, many studies will classify people into various levels of caffeine exposure on the basis of how much coffee they drink. Although coffee is the major source of caffeine for most people, failure to ask about other sources of caffeine consumption can lead to serious errors. A rabid Diet Coke drinker might mistakenly be classified into the low caffeine consumption group (Brown 2001).

Dietary studies will sometimes rely on household food surveys, but these need adjustment for the varying consumption of individual family members. For example, within the same family, males (especially boys aged 11–17 years) will have higher average intakes of calories and nutrients (Nelson 1986).

1.4.2 The case-control study

A case-control study selects patients on the basis of an outcome, such as development of breast cancer, and are compared to a group of patients without that outcome. Do the cases differ from the controls in some exposures?

Example: In a study of asthma deaths (Anderson 2005), researchers selected 532 patients who died between 1994 and 1998 with asthma mentioned in part I of the death certificate. For each asthma death, a similar asthma admission (without death) was identified at the same hospital, with a similar admission date and a similar age.

Example: In a study of vascular dementia (Chan Carusone 2004), researchers selected 28 patients with vascular dementia who were enrolled in the Geriatric Clinic at Henderson Hospital in Hamilton, Ontario, between July 1999 and October 2001. They also selected controls from a list of all caregivers at that clinic, regardless of the diagnosis of their spouse or family member, as long as the caregiver did not have any signs of dementia or stroke. Caregivers were matched by age (within 5 years) and sex. The researchers tested both cases and controls for Chalamydia.

A case-control study is very efficient in studying rare diseases. With this design, you round up all of the limited number of cases of the disease and then find a comparable control group. By contrast, a cohort design has to round up far more exposures to ensure that a handful of them will develop the rare disease.

Case-control studies do not perform well when you are evaluating a diagnostic test. They are easy to set up, because you have a group of patients with the disease and you estimate the probability of a positive result for the diagnostic test in this group (sensitivity). You also have a control group and you estimate the probability of a negative result for the diagnostic test in this group (specificity). Unfortunately, the case-control design usually has a collection of very obviously diseased patients among the cases and very obviously healthy patients among the controls. This is an example of spectrum bias (Ransohoff 1978), the lack of patients in the ambiguous middle of the spectrum. A study with spectrum bias will often overstate the sensitivity and specificity of a diagnostic test.

Example: A study of the rapid dipstick test for urinary tract infection (Lachs 1992), the sensitivity of the test was very good (92%) when restricted to a sample of patients with obvious signs of infection, but was poor (56%) when patients with more subtle manifestations of the disease were evaluated.

The case-control study is always retrospective because the outcome in a case-control study has already occurred. Retrospective studies usually have more problems with data quality because our memory is not always perfect.

What is worse is that sometimes the ability to remember is sharply influenced by the outcome being studied. People who experience a tragic event like a miscarriage will have a strong desire to try to understand why this has happened and will search their past for risk factors that have been highly publicized in the press (Bryant 1989). They do not make things up, but the problem is that the people in the control group only seem to remember about half the things that have happened in their past. This selective underreporting in the control group is known as recall bias and it can lead to some serious faulty findings.

If you have ‘leaky groups’ in a case-control design, this can cause problems also. Do some of the disease outcomes get left out of the cases? It might be harder, for example, to identify the less serious examples of disease.

Patients with milder forms of Alzheimer’s disease may not bother to seek out help. Only when the disease progresses enough to interfere with these patients’ ability to live and function independently will you encounter such patients. Watch out also for situations where healthy people or people with the incorrect disease are accidentally classified as cases. You can avoid problems with leaky groups if there is some type of registry that allows the researchers to identify every possible case.

The other major problem with this type of study is that it is so hard to find a good control group. You want to find controls that are identical to the cases in all aspects except for the outcome itself. When there is a roster of all potentially eligible subjects (subjects who would be classified as cases if they developed the disease), then selection of a good quality control group is easy (Wacholder 1995). Most studies would not have such a roster. In this case, the controls are often patients admitted to the hospital for outcomes unrelated to the study. So if cases represent newly diagnosed lung cancer, then the controls might be patients admitted for a bone fracture. Other times, you might ask the case to bring a friend with them or to identify a relative.

Selection of controls in a case-control study is difficult enough, but you also have to worry about the selection of the cases. Do you select incident cases (e.g. all breast cancer patients newly diagnosed during a given time frame) or prevalent cases (e.g. all breast cancer patients who are alive during a given time frame)? Selecting prevalent cases can lead to a very different answer than selecting incident cases. The probability of finding a case in a given time frame is related to mortality risk. Those patients who have a mild form of disease and survive for a relatively long time have a good chance of being around on the date that you go looking for them. Those patients who die quickly are unlikely to be around on the date that you go looking for them. A hypothetical example (Grimes 2002) involves a study of the relationship between snow shoveling and heart attacks. If such a study were done in a hospital setting, it would miss all the cases that died in their driveways. In general, selection of prevalent cases will lead to the selection of the milder and less rapidly fatal forms of the disease. A more detailed discussion of prevalence and incidence appears in Chapter 6.

Finally, the case-control design just does not sit well with your intuition. You are trying to find factors that cause an outcome, so you are sampling from the causes while a cohort design samples from the effects. Don’t let this bother you too much, though. The mathematics that justify the case-control design were developed half a century ago (Cornfield 1951) and careful use of the case-control design has helped answer important clinical questions which could not have been answered by other research designs.

Case-control designs, for example, established the use of aspirin as a cause of Reye’s syndrome (Monto 1999). It is hard to imagine how a randomized trial for Reye’s syndrome could have been done, because you would have to tell parents that you suspected, but were not quite sure, that giving an aspirin to a feverish child might lead to some pretty bad outcomes. So would you mind terribly if we recruited your son/daughter to participate in a trial where there is a 50% chance that they would get this possibly harmful substance?

1.4.3 The cross-sectional study

In contrast to the cohort and the case-control design, the cross-sectional study selects on the basis of neither exposure nor outcome. With the cross-sectional design, you select a single group of patients and simultaneously assess both their exposure variables and their outcome variables.

Example: In a study of intimate partner violence (Malcoe 2004), 312 Native American women attending a tribally operated clinic filled out a survey form. The survey included a modified Conflict Tactics Scale to assess whether the women experienced verbal or psychological aggression, or physical or sexual assault. The survey also asked about educational attainment, employment status, receipt of food stamps, and other questions to help determine their socioeconomic status. Since both the outcome (intimate partner violence) and the exposure (socioeconomic status) were determined at the same time, this represents a cross-sectional survey.

Example: In a study of respiratory problems (Salo 2004), 5,051 seventh grade students in Wuhan, China, completed a self-administered questionnaire. These students were classified according to six respiratory outcomes (wheezing with colds, wheezing without colds, bringing up phlegm with colds, bringing up phlegm without colds, coughing with colds, coughing without colds) and two exposure variables (coal burning for cooking and cleaning, and smoking in the home). Students were not randomly assigned to an exposure; so this is an observational study. Both the outcome variables and the exposure variables were assessed at a single point in time, so this represents a cross-sectional study.

Since there is no separation in time between assessment of exposure and assessment of outcome, you often cannot determine which came first. This loss of temporality makes it difficult to infer a cause-and-effect relationship. A hypothetical example of patient height (Mann 2003), describes how a cross-sectional study might notice a negative association between height and age. Could this be because people shrink as they age, or perhaps successive generations of people are taller because of the improvements in nutrition, or perhaps taller people just die earlier? With a cross-sectional study, you cannot easily disentangle these alternate explanations.

Be cautious about leaky groups again. Will the selection process in a cross-sectional study correctly identify exposures and outcomes? In particular, are patients with more serious illnesses easier/harder to capture in the cross-sectional study than patients with milder forms of the illness? Cross-sectional studies are fast, though, as you do not have to wait around to see what happens to the patients. These studies also allow you to easily explore relationships between multiple exposure variables and/or multiple outcome variables. But unlike the cohort design, which is useful for rare exposures, or the case-control design, which is useful for rare outcomes, the cross-sectional study is only effective if both the exposure and the outcome are relatively common events.

In general, the cross-sectional study is more useful as an exploratory tool, and can lead to the preparation of more definitive research studies with more rigorous designs.

Footnote: A lot of books on research will intentionally contrast cross-sectional and longitudinal designs. I do not mention longitudinal designs explicitly in this section because these do not fit into the hierarchy as I have described it. In general, a longitudinal design is usually a cohort design, with evaluation of the outcome at multiple time points. As such, it shares all the strengths and weaknesses of the cohort design. An additional strength of the longitudinal design, though, is that you can often gain considerable power for comparisons within a patient because you have removed between-patient variability from the equation. In this sense it is much like the crossover designs discussed in section 1.5.5.

1.4.4 The historical controls study

In a historical controls study, researchers will assign all of the research subjects to the new therapy. The outcomes of these subjects are compared to historical records representing the standard therapy.

Example: In a study of the rapid parathyroid hormone test (Johnson 2001), 49 patients undergoing parathyroidectomy received the rapid test. These patients were compared to 55 patients undergoing the same procedure before the rapid test was available. This is an observational study because the calendar, not the researchers, determined which test was applied. This particular observational study is a historical controls design because the control group represents patients tested before the availability of the rapid test.

The very nature of a historical controls study guarantees that there will be a major covariate imbalance between the two groups. Thus, you have to consider any factors that have changed over time that might be related to the outcome. To what extent might these factors affect the outcome differentially? For the most part, historical controls are considered one of the weakest forms of evidence. The one exception is when a disease has close to 100% mortality. In that situation, there is no need for a concurrent control group, since any therapy that is remotely effective can readily be detected. Even in this situation, you want to be sure there is a biological basis for the treatment and that the disease group is homogeneous.

1.4.5 Nonrandomized studies: What to look for

For studies using a cohort design:

Is the method for determining the exposure and control groups objective and accurate?

Some covariate imbalances are inevitable, but are any of them serious?

For studies using a case-control design:

Excluding the disease outcome itself, does the control group have similar features to the cases?

Were some outcomes missed or were some healthy people accidentally included as cases?

Is there a tendency for cases to have better recall of exposures than controls?

For studies using a cross-sectional design:

Are patients with more serious disease harder to capture in this research design?

Is there ambiguity about whether the exposure temporally precedes the disease?

For studies using a historical controls design:

Did the authors provide a justification for this approach?

In the time between the collection of the control group data and the treatment data, what other factors might have changed?

For all studies:

How successful were the researchers in selecting a representative control group?

Were there leaky groups: errors made in determining who had the exposure or in who had the disease outcome?

This webpage was written by Steve Simon on (unknown date), edited by Steve Simon, and was last modified on 2008-07-08. Send feedback to ssimon at cmh dot edu or click on the email link at the top of the page. Category: Statistical evidence

Stats >> Training >> Stats #32b: Practice Exercises

1. Review the following abstracts and identify the type of observational study (cohort, case-control, cross-sectional, or historical control).

1. Body fatness during childhood and adolescence and incidence of breast cancer in premenopausal women: a prospective cohort study. Heather J Baer, Graham A Colditz, Bernard Rosner, Karin B Michels, Janet W Rich-Edwards, David J Hunter and Walter C Willett. Breast Cancer Research 2005, 7:R314-R325 doi:10.1186/bcr998. Introduction Body mass index (BMI) during adulthood is inversely related to the incidence of premenopausal breast cancer, but the role of body fatness earlier in life is less clear. We examined prospectively the relation between body fatness during childhood and adolescence and the incidence of breast cancer in premenopausal women. Methods Participants were 109,267 premenopausal women in the Nurses' Health Study II who recalled their body fatness at ages 5, 10 and 20 years using a validated 9-level figure drawing. Over 12 years of follow up, 1318 incident cases of breast cancer were identified. Cox proportional hazards regression was used to compute relative risks (RRs) and 95% confidence intervals (CIs) for body fatness at each age and for average childhood (ages 5–10 years) and adolescent (ages 10–20 years) fatness. Results Body fatness at each age was inversely associated with premenopausal breast cancer incidence; the multivariate RRs were 0.48 (95% CI 0.35–0.55) and 0.57 (95% CI 0.39–0.83) for the most overweight compared with the most lean in childhood and adolescence, respectively (P for trend < 0.0001). The association for childhood body fatness was only slightly attenuated after adjustment for later BMI, with a multivariate RR of 0.52 (95% CI 0.38–0.71) for the most overweight compared with the most lean (P for trend = 0.001). Adjustment for menstrual cycle characteristics had little impact on the association. Conclusion Greater body fatness during childhood and adolescence is associated with reduced incidence of premenopausal breast cancer, independent of adult BMI and menstrual cycle characteristics. http://breast-cancer-research.com/content/7/3/R314

2. Impact of a nurses' protocol-directed weaning procedure on outcomes in patients undergoing mechanical ventilation for longer than 48 hours: a prospective cohort study with a matched historical control group. Jean-Marie Tonnelier, Gwenaël Prat, Grégoire Le Gal, Christophe Gut-Gobert, Anne Renault, Jean-Michel Boles and Erwan L'Her. Critical Care 2005, 9:R83-R89 doi:10.1186/cc3030. Introduction The aim of the study was to determine whether the use of a nurses' protocol-directed weaning procedure, based on the French intensive care society (SRLF) consensus recommendations, was associated with reductions in the duration of mechanical ventilation and intensive care unit (ICU) length of stay in patients requiring more than 48 hours of mechanical ventilation. Methods This prospective study was conducted in a university hospital ICU from January 2002 through to February 2003. A total of 104 patients who had been ventilated for more than 48 hours and were weaned from mechanical ventilation using a nurses' protocol-directed procedure (cases) were compared with a 1:1 matched historical control group who underwent conventional physician-directed weaning (between 1999 and 2001). Duration of ventilation and length of ICU stay, rate of unsuccessful extubation and rate of ventilator-associated pneumonia were compared between cases and controls. Results The duration of mechanical ventilation (16.6 ± 13 days versus 22.5 ± 21 days; P = 0.02) and ICU length of stay (21.6 ± 14.3 days versus 27.6 ± 21.7 days; P = 0.02) were lower among patients who underwent the nurses' protocol-directed weaning than among control individuals. Ventilator-associated pneumonia, ventilator discontinuation failure rates and ICU mortality were similar between the two groups. Discussion Application of the nurses' protocol-directed weaning procedure described here is safe and promotes significant outcome benefits in patients who require more than 48 hours of mechanical ventilation. http://ccforum.com/content/9/2/R83

3. Extravascular lung water in patients with severe sepsis: a prospective cohort study. Greg S Martin, Stephanie Eaton, Meredith Mealer and Marc Moss. Critical Care 2005, 9:R74-R82 doi:10.1186/cc3025. Introduction Few investigations have prospectively examined extravascular lung water (EVLW) in patients with severe sepsis. We sought to determine whether EVLW may contribute to lung injury in these patients by quantifying the relationship of EVLW to parameters of lung injury, to determine the effects of chronic alcohol abuse on EVLW, and to determine whether EVLW may be a useful tool in the diagnosis of acute respiratory distress syndrome (ARDS). Methods The present prospective cohort study was conducted in consecutive patients with severe sepsis from a medical intensive care unit in an urban university teaching hospital. In each patient, transpulmonary thermodilution was used to measure cardiovascular hemodynamics and EVLW for 7 days via an arterial catheter placed within 72 hours of meeting criteria for severe sepsis. Results A total of 29 patients were studied. Twenty-five of the 29 patients (86%) were mechanically ventilated, 15 of the 29 patients (52%) developed ARDS, and overall 28-day mortality was 41%. Eight out of 14 patients (57%) with non-ARDS severe sepsis had high EVLW with significantly greater hypoxemia than did those patient with low EVLW (mean arterial oxygen tension/fractional inspired oxygen ratio 230.7 ± 36.1 mmHg versus 341.2 ± 92.8 mmHg; P < 0.001). Four out of 15 patients with severe sepsis with ARDS maintained a low EVLW and had better 28-day survival than did ARDS patients with high EVLW (100% versus 36%; P = 0.03). ARDS patients with a history of chronic alcohol abuse had greater EVLW than did nonalcoholic patients (19.9 ml/kg versus 8.7 ml/kg; P < 0.0001). The arterial oxygen tension/fractional inspired oxygen ratio, lung injury score, and chest radiograph scores correlated with EVLW (r2 = 0.27, r2 = 0.18, and r2 = 0.28, respectively; all P < 0.0001). Conclusions More than half of the patients with severe sepsis but without ARDS had increased EVLW, possibly representing subclinical lung injury. Chronic alcohol abuse was associated with increased EVLW, whereas lower EVLW was associated with survival. EVLW correlated moderately with the severity of lung injury but did not account for all respiratory derangements. EVLW may improve both risk stratification and management of patients with severe sepsis. http://ccforum.com/content/9/2/R74

4. Breast implants following mastectomy in women with early-stage breast cancer: prevalence and impact on survival. Gem M Le, Cynthia D O'Malley, Sally L Glaser, Charles F Lynch, Janet L Stanford, Theresa HM Keegan and Dee W West. Breast Cancer Res 2005, 7:R184-R193 doi:10.1186/bcr974. Background Few studies have examined the effect of breast implants after mastectomy on long-term survival in breast cancer patients, despite growing public health concern over potential long-term adverse health effects. Methods We analyzed data from the Surveillance, Epidemiology and End Results Breast Implant Surveillance Study conducted in San Francisco–Oakland, in Seattle–Puget Sound, and in Iowa. This population-based, retrospective cohort included women younger than 65 years when diagnosed with early or unstaged first primary breast cancer between 1983 and 1989, treated with mastectomy. The women were followed for a median of 12.4 years (n = 4968). Breast implant usage was validated by medical record review. Cox proportional hazards models were used to estimate hazard rate ratios for survival time until death due to breast cancer or other causes for women with and without breast implants, adjusted for relevant patient and tumor characteristics. Results Twenty percent of cases received postmastectomy breast implants, with silicone gel-filled implants comprising the most common type. Patients with implants were younger and more likely to have in situ disease than patients not receiving implants. Risks of breast cancer mortality (hazard ratio, 0.54; 95% confidence interval, 0.43–0.67) and nonbreast cancer mortality (hazard ratio, 0.59; 95% confidence interval, 0.41–0.85) were lower in patients with implants than in those patients without implants, following adjustment for age and year of diagnosis, race/ethnicity, stage, tumor grade, histology, and radiation therapy. Implant type did not appear to influence long-term survival. Conclusions In a large, population-representative sample, breast implants following mastectomy do not appear to confer any survival disadvantage following early-stage breast cancer in women younger than 65 years old. http://breast-cancer-research.com/content/7/2/R184

5. Pregnancy weight gain and breast cancer risk. Tarja I Kinnunen, Riitta Luoto, Mika Gissler, Elina Hemminki and Leena Hilakivi-Clarke. BMC Women's Health 2004, 4:7 doi:10.1186/1472-6874-4-7. Background Elevated pregnancy estrogen levels are associated with increased risk of developing breast cancer in mothers. We studied whether pregnancy weight gain that has been linked to high circulating estrogen levels, affects a mother's breast cancer risk. Methods Our cohort consisted of women who were pregnant between 1954–1963 in Helsinki, Finland, 2,089 of which were eligible for the study. Pregnancy data were collected from patient records of maternity centers. 123 subsequent breast cancer cases were identified through a record linkage to the Finnish Cancer Registry, and the mean age at diagnosis was 56 years (range 35 – 74). A sample of 979 women (123 cases, 856 controls) from the cohort was linked to the Hospital Inpatient Registry to obtain information on the women's stay in hospitals. Results Mothers in the upper tertile of pregnancy weight gain (>15 kg) had a 1.62-fold (95% CI 1.03–2.53) higher breast cancer risk than mothers who gained the recommended amount (the middle tertile, mean: 12.9 kg, range 11–15 kg), after adjusting for mother's age at menarche, age at first birth, age at index pregnancy, parity at the index birth, and body mass index (BMI) before the index pregnancy. In a separate nested case-control study (n = 65 cases and 431 controls), adjustment for BMI at the time of breast cancer diagnosis did not modify the findings. Conclusions Our study suggests that high pregnancy weight gain increases later breast cancer risk, independently from body weight at the time of diagnosis. http://www.biomedcentral.com/1472-6874/4/7

6. Racial variations in processes of care for patients with community-acquired pneumonia. Eric M Mortensen, John Cornell and Jeff Whittle. BMC Health Services Research 2004, 4:20 doi:10.1186/1472-6963-4-20. Background Patients hospitalized with community acquired pneumonia (CAP) have a substantial risk of death, but there is evidence that adherence to certain processes of care, including antibiotic administration within 8 hours, can decrease this risk. Although national mortality data shows blacks have a substantially increased odds of death due to pneumonia as compared to whites previous studies of short-term mortality have found decreased mortality for blacks. Therefore we examined pneumonia-related processes of care and short-term mortality in a population of patients hospitalized with CAP. Methods We reviewed the records of all identified Medicare beneficiaries hospitalized for pneumonia between 10/1/1998 and 9/30/1999 at one of 101 Pennsylvania hospitals, and randomly selected 60 patients at each hospital for inclusion. We reviewed the medical records to gather process measures of quality, pneumonia severity and demographics. We used Medicare administrative data to identify 30-day mortality. Because only a small proportion of the study population was black, we included all 240 black patients and randomly selected 720 white patients matched on age and gender. We performed a resampling of the white patients 10 times. Results Males were 43% of the cohort, and the median age was 76 years. After controlling for potential confounders, blacks were less likely to receive antibiotics within 8 hours (odds ratio with 95% confidence interval 0.6, 0.4–0.97), but were as likely as whites to have blood cultures obtained prior to receiving antibiotics (0.7, 0.3–1.5), to have oxygenation assessed within 24 hours of presentation (1.6, 0.9–3.0), and to receive guideline concordant antibiotics (OR 0.9, 0.6–1.7). Black patients had a trend towards decreased 30-day mortality (0.4, 0.2 to 1.0). Conclusion Although blacks were less likely to receive optimal care, our findings are consistent with other studies that suggest better risk-adjusted survival among blacks than among whites. Further study is needed to determine why this is the case. http://www.biomedcentral.com/1472-6963/4/20