Stats #32a: Statistical Evidence. Apples or oranges? Randomized studies.

Stats #32a: Statistical Evidence: Apples or Oranges? Randomized studies.

Content: 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.

Objectives: In this class you will learn how to:

create a randomized list of treatments;
understand the practical and ethical limitations to randomized studies; and
describes three variations on randomization.

Teaching strategies: Didactic lectures and small group exercises.

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

Outline:

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. Randomized 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. Randomized studies.

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

What is randomization? One way to avoid most of the problems with imbalanced covariates is to use randomization. Randomization is the assignment of treatment groups through the use of a random device, like the flip of a coin or the roll of a die, or numbers randomly generated by a computer. Randomization is not always possible, practical, or ethical. But when you can use randomization, it greatly adds to the credibility of the research study.

Example: In a study of treatments for osteoarthritis of the knee (Teekachunhatean 2004), 200 patients suffering from osteoarthritis of the knee were randomly assigned to receive either DJW (Duhuo Jisheng Wan, a Chinese herbal remedy) and a placebo for diclofenac or diclofenac and a placebo for DJW. Patients were evaluated on visual analog scale (VAS) score that assessed pain and stiffness, Lequesne’s functional index, time for climbing up ten steps, as well as physician’s and patients’ overall opinions on improvement.

Example: In a study of critical appraisal skills training (Taylor 2004), 145 health professionals were randomly assigned to either receive immediate training in a half-day critical appraisal skills workshop or were placed on a waiting list for a future workshop. These subjects were evaluated on knowledge attitudes and behaviors relating to evidence-based medicine.

In both studies the researchers decided who got what. This is a hallmark of a randomized design and it only can occur when the patients and/or their doctors have no say in the assignment. This is an incredible gift that patients in a research study offer you. They sacrifice their ability to choose among two or more therapies and instead let that choice be decided by the flip of a coin.

Randomization helps ensure that both measurable and immeasurable factors are balanced out across both the standard and the new therapy, assuring a fair comparison. Used correctly, it also guarantees that no conscious or subconscious efforts were used to allocate subjects in a biased way. There are situations where covariate imbalance can appear, even in a well-randomized study (Roberts 1999). Just as you have no guarantee that a flip of 100 coins will yield exactly 50 heads and 50 tails, you have no guarantee that covariate imbalances cannot creep into a randomized study once in a while. This is not just a theoretical concern. One article (Mann 2002) argues that a difference in baseline stroke severity in a randomized trial of tPA produced an incorrect assertion of the effectiveness of this treatment.

Randomization relies on the law of large numbers. With small sample sizes, covariate imbalance may still sneak in. A study examining the probability of covariate imbalance (Hsu 1989) showed that total sample sizes less than 10 could have a 50% chance or higher of having a categorical covariate with levels twice as large in one group than the other. This study also showed that total sample sizes of 40 or greater would have very little chance of such a serious imbalance, and a total of 20–40 subjects would be acceptable if there were only one or two important covariates.

A fishy story about randomization. I was told this story but have no way of verifying its accuracy. It is one of those stories that if it is not true, it should be. A long, long, time ago, a research group wanted to examine a pollutant to find concentration levels that would kill fish. This research required that 100 fish be separated into five tanks, each of which would get a different level of the pollutant. The researchers caught the first 20 fish and put them in the first tank, then put the next 20 fish in a second tank, and so forth. The last 20 fish went into the fifth tank. Each fish tank got a different concentration of the pollutant. When the research was done, the mortality was related not to the dosage, but to the order in which the tanks were filled, with the worst outcomes being in the first tank filled and the best outcomes in the last tank filled. What happened was that the slow-moving, easy-to-catch fish (the weakest and most sickly) were all allocated to the first tank. The fast-moving, hard-to-catch fish (the strongest and healthiest) ended up in the last tank.

Failure to randomize in this study ruined the entire effort. The huge imbalance caused by putting the sickest fish in the first tank and the healthiest fish in the last tank overwhelmed any differences in mortality caused by varying levels of the pollutant.

Random assignment means that the choice is left to some device that is inherently random and unpredictable. A flip of a coin is one approach, but usually a table of random numbers or a random number generator is more practical. I cannot think of anything more boring than flipping a coin 200 times.

Step 1. Arrange
your data in a
systematic order. Step 2. Attach
a column of
random numbers. Step 3. Sort by
the column of
random numbers.

T
C
T
C
T
C
T
C T    0.608
C    0.739
T    0.831
C    0.016
T    0.759
C    0.877
T    0.830
C    0.030 C    0.016
C    0.030
T    0.608
C    0.739
T    0.759
T    0.830
T    0.831
C    0.877

The table shown above illustrates the simplest way to randomize an experiment. The trick is to recognize that sorting by a column of random numbers puts the data in a random order.

You can apply this trick to other situations where randomization is needed. Suppose, for example, that you have a list of 100 patients and you want to select 25 of them to send a survey to. Just list the patients in alphabetical order. Attach a random number to each patient’s name. Then sort the patient list by the random number. This puts the patient names in a random order, and you select the first 25 names on the list. If one of the patients turns out to be ineligible, then just go to the 26th name on the list.

Often researchers will use block randomization. This approach creates randomization within small blocks, usually every 6 to 10 patients. This guarantees that your list will retain exact balance at the end of each block and will only show small degrees of imbalance in between. In contrast, randomization across an entire very long list will show some random drift which would lead to serious imbalances partway through the study. If the experiment ends early, block randomization will ensure a greater degree of balance than simple randomization.

Concealing the randomization list. Another important aspect of randomization is concealed allocation, which is withholding the randomization list from those involved with recruiting subjects. This concealment occurs until after subjects agree to participate and the recruiter determines that the patient is eligible for the study. Only then is a sealed envelope opened that reveals the treatment status. Concealed allocation can also be done through a special phone number that the doctor calls to discover the treatment status.

Please note that concealing the randomization list is not the same as blinding the study. Certain treatments, such as surgery, cannot be blinded but the allocation list can still be concealed.

Consider, for example, a randomized trial comparing laparoscopic surgery to traditional surgery. After the fact, the patient can tell by the size of the scar what type of surgery they received. But the choice as to what type of surgery that the patient receives could be made as the patient is being sedated. There is an example of a research study where a sterilized coin was flipped in the operating room to decide which surgery will be used (Hollis 1999).

If the randomization list is not concealed, doctors have the ability to consciously or unconsciously influence the composition of the groups. They can do this by applying exclusion criteria differentially or by delaying entry of a certain healthier (or unhealthier) subject so he/she gets into the ‘desirable’ group. Unblinded allocation schemes tend, on average to overstate the effectiveness of the new therapy by 30–40% (Schulz 1996).

There are many stories of physicians who have tried and succeeded in recruiting a patient into a preferred group. If the treatment allocation is hidden in sealed envelopes, they can hold it up to a strong light. If the sealed envelopes are not sequentially numbered, they can open several envelopes at once. If the allocation is controlled by a central operator, they can call and ask for the allocation of several patients at once.

When a doctor has an overt preference to enroll a patient into one group over another, it raises ethical issues and perhaps the doctor should not be participating in the trial. You should only participate in a research study if you believe there is genuine uncertainty about whether the new therapy or the standard therapy is better. If not, you have no business participating in a study where some of your patients will be randomized to a treatment that you consider inferior. Unfortunately, some doctors will continue to participate in these trials but will try to skew the enrollment of some or all of the patients towards a favored therapy.

Concealed allocation only makes sense for a truly randomized study. If patients are assigned in an alternating fashion, concealed allocation is buying a fancy burglar alarm and leaving the front door wide open. As you will see in the next section, alternating assignments is a bad idea, but it is even worse because the doctors will immediately recognize the next patient is going to be allocated to. This makes it easy for them to preferentially recruit to a specific treatment if they want to.

Ethical and practical constraints on randomization. There are many situations where randomization is not practical or possible. Sometimes patients have a strong preference for one particular treatment and would not consider the possibility of being randomized into a different treatment. Surgery is one area with strong patient preferences especially for newer approaches like laparoscopic surgery (Lefering 2003).

Randomization is also problematic for interventions that are already known to be effective. While further research would help better define these advantages, you cannot ask half of your patients to sacrifice the benefits of the new intervention. A good example of this is breastfeeding, which has a whole host of positive effects. There is still ongoing research to identify and better quantify these and other benefits (A nice summary of these benefits is available at: www.breastfeeding.com/all_about/all_ about_more.html), but almost none of this research is randomized (Kramer 2002 is a notable exception). Some nonrandomized studies of the relationship between breastfeeding and intelligence have failed to account for the fact that the breastfeeding mothers tend to be better educated, have higher socioeconomic status and that their babies tend to grow up in an environment that has greater overall levels of stimulation (Jain 2002). Still, it would be unethical to ask a random half of new mothers to sacrifice the benefits of breastfeeding. While this sometimes leads to limitations on what you can infer from these studies, that is, the price you pay to live in an ethical society.

Randomization also does not work when you are studying noxious agents, like second-hand cigarette smoke or noisy workplaces. It would be unethical to deliberately expose people to any of these agents, so we have

Sometimes, the sample sizes required or the duration of the study make it difficult to use randomization. Diseases like cancer that have a long latency period are especially hard to study with a randomized design.

Retrospective studies, where the outcome of interest has already occurred and/or you are looking at factors in the past that might have caused this outcome, are also impossible to randomize, unless you have a time machine. (See Leibovici 2001 for an amusing exception to this rule, though.) Sometimes, the groups being studied existed before the start of the research. Genetic conditions like Down’s syndrome cannot be randomly assigned to half of the patients in your study. I like to think of these situations as cases where God does the randomization.

Sometimes researchers just do not want to go to the effort of randomizing. If you assign the treatment or therapy, rather than letting the patients and their doctors choose, you have to expend a lot of energy. Is it worth the effort? It is usually faster and cheaper to use existing nonrandomized databases. You get a lot larger sample size for your money. Depending on the situation, that might be enough to counterbalance the advantages of randomization.

A nonrandomized study might also be a useful prelude in the planning of an expensive randomized trial. The nonrandomized trial would help you better understand and prepare for the resource requirements and familiarize your staff with the mechanics of treating and evaluating your research subjects.

Variations on randomization. There are three variations to randomization where the researchers have control over treatment assignment, but they use something other than a table of random numbers for the assignment. The first approach, minimization, is a credible and reasonable choice, but the other two approaches, alternating assignment and haphazard assignment, do not have much to recommend them.

Minimization. An alternative, when the researchers have sufficient control, is to allocate the assignments so that at each step, the covariate imbalance is minimized.

So if the treatment group has a slight surplus of older patients and the next patient to join the study is also older than average, then that patient would be assigned to the control group so as to reduce the age discrepancy.

Example: In a study of behavioral counseling (Steptoe 1999), twenty general practices were allocated either to use behavioral counseling based on the stages of change model for all their patients, or no counseling other than what their current standard of care. These practices were assigned using minimization to ensure balance on three factors: the degree of underprivileged patients being served, the patient to nurse ratio of the practice, and fund holding status.

Minimization is a good approach if there are one or two covariates which are especially important and which are easily measured at the start of the study. It will perform better than randomization on those factors, although there is no guarantee of covariate balance for other covariates not used in the minimization. Minimization also cannot control for unmeasured covariates.

There is more effort required in setting up a study with minimization. You need a computer to be available at the time and location of the recruitment of each patient because you cannot just print a list ahead of time. Another difficulty is that minimization is open to possible abuse because doctors might be able to predict what the next assignment would be.

Alternating assignments. Another approach used in place of randomization is to alternate the assignment, so that every even patient is in the treatment group and every odd patient is in the control group. Alternating assignment was popular in trials before World War II; it was felt that researchers would not understand and not tolerate randomization (Yoshioka 1998).

Example: In a study of patients with cystic fibrosis (Homnick 1999), the first patient was randomly assigned either manual chest physiotherapy, or a flutter device to treat acute pulmonary exacerbation. After the first patient, each additional patient was assigned to the alternate approach.

Example: In a study of patients with penetrating eye injuries (Lakits 1998), patients were assigned alternately to either helical computed tomography or conventional computed tomography. Images were assessed for the ability to detect and accurately localize foreign bodies.

Alternating assignment seems on the surface to be a good approach, but it can sometimes lead to trouble. This is especially true when one patient has a direct or indirect influence on the next patient. You may have seen this level of influence if you grow vegetables in a garden. If you have a row of cabbages, for example, you will often see a pattern of big cabbage, little cabbage, big cabbage, little cabbage, etc. What happens, if the cabbages are planted a bit too closely, is that one of the cabbages will grow just a bit faster at first. It will extend into the neighboring cabbage’s territory, stealing some of the nutrients and water, and thus growing even faster at the expense of the neighbor. If you assigned a fertilizer to every other cabbage, you would probably see an artificial difference because of the alternating pattern in growth within a row.

This alternating pattern can also occur in medicine. Consider, for example, a study of howmuch time doctors spend with their patients. If the first patient takes longer than expected, the doctor will probably rush a bit with the second patient in order to keep from falling further behind schedule. On the other hand, if the first patient finishes quickly, then the doctor will feel more relaxed and might tend to take a bit more time with the next patient.

In some situations, alternating assignment would be tolerable, but there is no good reason to prefer this over random assignment. You should be skeptical of this approach because studies with alternating assignment will tend, on average, to overstate the effectiveness of a new therapy by 15% (Colditz 1989).

Haphazard assignment. Other choices that researchers will make it to base assignments on some arbitrary value. Often it is the evenness/oddness of the arbitrary number that determines the treatment assignment. For example, patients born on even-numbered dates would be assigned to the treatment group and those born on odd-numbered dates would be assigned to the control group. Some months have more odd days than even days (actually my life seems to have more than its fair share of odd days). This is a nitpick, but more importantly, an arbitrary or haphazard number is never going to be as good as a purely random number. The haphazard assignment will always cast a shadow of doubt over the research study. This is a shame, because almost every study with haphazard assignment could have been run as a randomized study with just a little more fuss.

Example: In a study of heparinized saline to maintain the patency of patient catheters (Kulkarni 1994), patients admitted on odd-numbered dates received heparinized saline and patients admitted on even-numbered dates received normal saline.

Example: In a study of supplemental oxygen treatment for the treatment of stroke (Ronning 1999), patients born on even days were assigned to the supplemental oxygen group and patients born on odd days were assigned to the control group.

Example: In a study of interview methods for measuring risk behavior in injecting drug users (Des Jarlais 1999), patients were assigned either to a face-to-face interview or to audio-computer-assisted self-interviewing, depending on which week it was. The interview approach alternated from week to week. The patients were assessed to see if reporting of HIV risk behaviors changes between the interview methods.

In some situations, haphazard assignment might be tolerable, but there is no good reason to use this approach. The first study mentioned above was excluded from a meta-analysis of heparinized saline (Randolph 1998) because the reviewers felt the quality level was too low.

Summary If a study is randomized, look for the following features: . Was there a description of the source of randomness. Did the researchers use a table of random numbers? Did they use a computer to generate random numbers? . Did the researchers conceal the randomization list from the doctors during the recruitment of patients?

When a study was not randomized, look for the following features: For a study using minimization: . Which covariates were used to assess balance? . Were any important covariates ignored? For studies using alternating assignments or haphazard assignments: . Did the authors provide a justification for this approach? . What possible artificial patterns in the assignments might create an artefactual relationship with the treatment assignment?

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 #32a: Practice Exercises

1. Review the following abstracts, all from studies where randomization was not done. Speculate on the reason that randomization was not performed.

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

2. Review the same set of abstracts. Identify the type of observational study (cohort, case-control, historical control).