The first type of QED highlighted in this review is perhaps the most straightforward type of intervention design: the pre-post comparison study with a non-equivalent control group. In this design, the intervention is introduced at a single point in time to one or more sites, for which there is also a pre-test and post-test evaluation period, The pre-post differences between these two sites is then compared. In practice, interventions using this design are often delivered at a higher level, such as to entire communities or organizations 1 [ Figure 1 here]. In this design the investigators identify additional site(s) that are similar to the intervention site to serve as a comparison/control group. However, these control sites are different in some way than the intervention site(s) and thus the term “non-equivalent” is important, and clarifies that there are inherent differences in the treatment and control groups ( 15 ).
Illustration of the Pre-Post Non-Equivalent Control Group Design
The strengths of pre-post designs are mainly based in their simplicity, such as data collection is usually only at a few points (although sometimes more). However, pre-post designs can be affected by several of the threats to internal validity of QEDs presented here. The largest challenges are related to 1) ‘history bias’ in which events unrelated to the intervention occur (also referred to as secular trends) before or during the intervention period and have an effect on the outcome (either positive or negative) that are not related to the intervention ( 39 ); and 2) differences between the intervention and control sites because the non-equivalent control groups are likely to differ from the intervention sites in a number of meaningful ways that impact the outcome of interest and can bias results (selection bias).
At this design stage, the first step at improving internal validity would be focused on selection of a non-equivalent control group(s) for which some balance in the distribution of known risk factors is established. This can be challenging as there may not be adequate information available to determine how ‘equivalent’ the comparison group is regarding relevant covariates.
It can be useful to obtain pre-test data or baseline characteristics to improve the comparability of the two groups. In the most controlled situations within this design, the investigators might include elements of randomization or matching for individuals in the intervention or comparison site, to attempt to balance the covariate distribution. Implicit in this approach is the assumption that the greater the similarity between groups, the smaller the likelihood that confounding will threaten inferences of causality of effect for the intervention ( 33 , 47 ). Thus, it is important to select this group or multiple groups with as much specificity as possible.
In order to enhance the causal inference for pre-post designs with non-equivalent control groups, the best strategies improve the comparability of the control group with regards to potential covariates related to the outcome of interest but are not under investigation. One strategy involves creating a cohort, and then using targeted sampling to inform matching of individuals within the cohort. Matching can be based on demographic and other important factors (e.g. measures of health care access or time-period). This design in essence creates a matched, nested case-control design.
Collection of additional data once sites are selected cannot in itself reduce bias, but can inform the examination of the association of interest, and provide data supporting interpretation consistent with the reduced likelihood of bias. These data collection strategies include: 1) extra data collection points at additional pre- or post- time points (to get closer to an interrupted time series design in effect and examine potential threats of maturation and history bias), and 2) collection of data on other dependent variables with a priori assessment of how they will ‘react’ with time dependent variables. A detailed analysis can then provide information on the potential affects on the outcome of interest (to understand potential underlying threats due to history bias).
Additionally, there are analytic strategies that can improve the interpretation of this design, such as: 1) analysis for multiple non-equivalent control groups, to determine if the intervention effects are robust across different conditions or settings (.e.g. using sensitivity analysis), 2) examination within a smaller critical window of the study in which the intervention would be plausibly expected to make the most impact, and 3) identification of subgroups of individuals within the intervention community who are known to have received high vs. low exposure to the intervention, to be able to investigate a potential “dose-response” effect. Table 2 provides examples of studies using the pre-post non-equivalent control group designs that have employed one or more of these improvement approaches to improve the internal study’s validity.
Improving Quasi-Experimental Designs-Internal and External Validity Considerations
Study/General Design | Intervention | Design Strategy to Improve Internal Validity | Design Strategy to Improve External Validity |
Pre-Post Designs with Non-Equivalent Control Group | |||
Cousins et al 2016 | Campus Watch program targeting problem drinking and violence at 1 university campus with 5 control campuses in New Zealand | • Standardization of independent repeat sampling, survey and follow-up methods across all sites (5 control and 1 intervention site) • 5 sites as controls studies aggregate and individually as controls • Consumption and harms data from national surveys to compare data trends over time | Over-sampling of indigenous groups to extend interpretation of findings |
Chronic disease management program with pharmacist-based patient coaching within a health care insurance plan in Cincinnati, US | • Matching of participants with non-participants on demographic and health care access measures (using propensity score matching) | ||
Distribution of bed nets to prevent malaria and reduce malaria mortality in Gambia 41 sites receiving intervention compared to external villages (which differed by size and ethnic distribution) | • Examination of data trends during the highest infection times of the year (i.e., rainy season vs dry season) to see if rates were higher then. • Detailed study of those using bed nets within intervention villages (i.e., guaranteed exposure “dose”, to examine dose-response in intervention arm | ||
Interrupted Time Series | |||
Study/General Design | Intervention | Design Strategy to Improve Internal Validity | Design Strategy to Improve External Validity |
Pellegrin 2016 Interrupted time series with comparison group | Formal transfer of high-risk patients being discharged from hospital to a community-based pharmacist follow-up program for up to 1 year post-hospitalization (6 intervention and 5 control sites) | • Long baseline period (12 pre-intervention data points) • Intervention roll-out staggered based on staff availability (site 1 had eight post-intervention data points while site 8 had two) | Detailed implementation-related process measures monitored (and provided to individual community-based pharmacists regarding their performance) over entire study period |
Robinson 2015 Interrupted time series without control group | New hospital discharge program to support high-risk patients with nurse telephone follow-up and referral to specific services (such as pharmacists for medication reconciliation and review) | • Additionally examined regression discontinuity during the intervention period to determine if the risk score used to determine eligibility for the program influenced the outcome | Measured implementation outcomes of whether the intervention was delivered with high fidelity to the protocols |
Interrupted time series with comparison group | Removal of direct payment at point of health care services for children under 5, very low income individuals and pregnant women re: consultations, medications and hospitalizations | Built into a pilot to collect control data, and then extend this work to include additional districts, one intervention and one non-intervention district, along with 6 additional years of observation. | Examined sustainability over 72 months of follow-up, and associations with clinic characteristics, such as density of workforce. |
Stepped Wedge Design | |||
Study/General Design | Intervention | Design Strategy to Improve Internal Validity | Design Strategy to Improve External Validity |
Non-randomized stepped wedge cluster trial | Site-level roll out of integrated antiretroviral treatment (ART) intervention in 8 public sector clinics, to achieve more rapid treatment initiation among women with HIV in Zambia, than the existing referral method used for initiation of treatment. | • The 8 sites were matched into four pairs based on the number of HIV-infected pregnant women expected in each site. • The intervention roll out was done for one member of the least busy pair, one member of the second busiest pair, one member of the third busiest pair, and one member of the busiest pair. Rollout to the remaining pairs proceeded in reverse order. • A transition cohort was established that was later excluded from the analysis. It included women who were identified as eligible in the control period of time close to the time the intervention was starting. | |
See also: Randomized stepped wedge cluster trial | Multi-faceted quality improvement intervention with a passive and an active phase among 6 regional emergency medical services systems and 32 academic and community hospitals in Ontario, Canada. The intervention focused on comparing interventions to improve the implementation of targeted temperature management following out-of-hospital cardiac arrest through passive (education, generic protocol, order set, local champions) versus additional active quality improvement interventions (nurse specialist providing site-specific interven- tions, monthly audit-feedback, network educational events, inter- net blog) versus no intervention (baseline standard of care). | : • Randomization at the level of the hospital, rather than the patient to minimize contamination, since the intervention targeted groups of clinicians. • Hospitals were stratified by number of Intensive Care Unit beds ((< 10 beds vs ≥ 10 beds as a proxy for hospital size). Randomization was done within strata. • Formalized a transition cohort for which a more passive intervention strategy was tested. This also allowed more time for sites to adopt all elements of the complex intervention before crossing over to the active intervention group. | Characterization of system and organizational factors that might affect adoption: Collection of longitudinal data relevant to implementation processes that could impact interpretation of findings such as academic vs community affiliation, urban vs rural (bed size) |
Randomized stepped wedge cluster trial | Seasonal malaria prophylaxis for children up to age 10 in central Senegal given to households monthly through health system staff led home visits during the malaria season. The first two phases of implementation focused on children under age 5 years and the last phase included children up to age 10 years, and maintained a control only group of sites during this period. | : • Constrained randomization of program roll-out across 54 health posts catchment areas and center-covered regions, • More sites received the intervention later stages (n=18) than in beginning (n=9). • To achieve balance within settings for potential confounders (since they did not have data on malaria incidence), such as distance from river, distance from health center, population size and number of villages, assessment of ability to implement. • Included nine clinics as control sites throughout the study period. | Characterization of factors that might affect usage and adherence made with longitudinal data: Independent evaluations of malaria prophylaxis usage, adherence, and acceptance were included prospectively, using routine health cards at family level and with external assessments from community surveys. In-depth interviews conducted across community levels to understand acceptability and other responses to the intervention Included an embedded study broadening inclusion criteria, to focus on a wider age group of at risk children |
Wait-list randomized stepped wedge design | Enrollment of 1,655 male mine employees with HIV infection randomized over a short period of time into an intervention to prevent TB infection (use of isoniazid preventive therapy), among individuals with HIV. Treatment was self-administered for 6 months or for 12 months and results were based on cohort analyses. | • Employees were invited in random sequence to attend a workplace HIV clinic. | Enumeration of at risk cohort and estimation of spill-over effect beyond those enrolled: Since they used an enrollment list, they were able to estimate the effect of the intervention (the provision of clinic services) among the entire eligible population, not just those enrolled in the intervention over the study period. |
Ratanawongsa et al; Handley et al 2011 Wait-list randomized stepped wedge design | Enrollment of 362 patients with diabetes into a health-IT enabled self-management support telephone coaching program, using a wait-list generated from a regional health plan, delivered in 3 languages. | • Patients were identified from an actively maintained diabetes registry covering 4 safety net health clinics in the United States, and randomized to receive the coaching intervention immediately or after 6 moths. • Patients were randomized to balance enrolment for English, Cantonese, and Spanish, over the study period. | External validity-related measures for acceptability among patients as well as fidelity measures, for the health IT-enabled health coaching intervention were assessed using a fidelity framework. |
Bailet et al 2011 | Literacy intervention for pre-kindergarten children at risk for reading failure in a southern US city administered in child care and pre-school sites, delivered twice a week for 9 weeks. For large sites, did not randomize at site level, but split the schools, so all children could be taught in the intervention period, either fall or spring. At-risk children in these “split” schools received intervention at only one of the two time points (as did their “non-split school” peers); however, the randomization to treatment group occurred at the child level. | • Random assignment of clusters (schools). • Matched pairs of child care centers by zip code and percentage of children receiving a state-sponsored financial subsidy. Within these groups random assignment to receive either immediate or deferred enrolment into the intervention. | External validity was enhanced in years 2–3 with a focus on teacher training for ensuring measures fidelity, completion of each week of the curriculum to enhance assessment of a potential dose-response. Refined intervention applied in years 2–3, based on initial data. |
Mexican Government randomly chose 320 early intervention and 186 late (approximately one year later) intervention communities in seven states for Oportunidades, which provided cash transfers to families conditional on children attending school and family members obtaining preventive medical care and attending —education talks on health-related topics. | : • More communities randomized to an early intervention period |
Cousins et al utilized a non-equivalent control selection strategy to leverage a recent cross-sectional survey among six universities in New Zealand regarding drinking among college-age students ( 16 ). In the original survey, there were six sites, and for the control group, five were selected to provide non-equivalent control group data for the one intervention campus. The campus intervention targeted young adult drinking-related problems and other outcomes, such as aggressive behavior, using an environmental intervention with a community liaison and a campus security program (also know as a Campus Watch program). The original cross-sectional survey was administered nationally to students using a web-based format, and was repeated in the years soon after the Campus Watch intervention was implemented in one site. Benefits of the design include: a consistent sampling frame at each control sites, such that sites could be combined as well as evaluated separately and collection of additional data on alcohol sales and consumption over the study period, to support inference. In a study by Wertz et al ( 48 ), a non-equivalent control group was created using matching for those who were eligible for a health coaching program and opted out of the program (to be compared with those who opted in) among insured patients with diabetes and/or hypertension. Matching was based on propensity scores among those patients using demographic and socioeconomic factors and medical center location and a longitudinal cohort was created prior to the intervention (see Basu et al 2017 for more on this approach).
In the pre-post malaria-prevention intervention example from Gambia, the investigators were studying the introduction of bed nets treated with insecticide on malaria rates in Gambia, and collected additional data to evaluate the internal validity assumptions within their design ( 1 ). In this study, the investigators introduced bed nets at the village level, using communities not receiving the bed nets as control sites. To strengthen the internal validity they collected additional data that enabled them to: 1) determine whether the reduction in malaria rates were most pronounced during the rainy season within the intervention communities, as this was a biologically plausible exposure period in which they could expect the largest effect size difference between intervention and control sites, and 2) examine use patterns for the bed nets, based on how much insecticide was present in the bed nets over time (after regular washing occurred), which aided in calculating a “dose-response” effect of exposure to the bed net among a subsample of individuals in the intervention community.
An interrupted time series (ITS) design involves collection of outcome data at multiple time points before and after an intervention is introduced at a given point in time at one or more sites ( 6 , 13 ). The pre-intervention outcome data is used to establish an underlying trend that is assumed to continue unchanged in the absence of the intervention under study ( i.e., the counterfactual scenario). Any change in outcome level or trend from the counter-factual scenario in the post-intervention period is then attributed to the impact of the intervention. The most basic ITS design utilizes a regression model that includes only three time-based covariates to estimate the pre-intervention slope (outcome trend before the intervention), a “step” or change in level (difference between observed and predicted outcome level at the first post-intervention time point), and a change in slope (difference between post- and pre-intervention outcome trend) ( 13 , 32 ) [ Figure 2 here].
Interrupted Time Series Design
Whether used for evaluating a natural experiment or, as is the focus here, for prospective evaluation of an intervention, the appropriateness of an ITS design depends on the nature of the intervention and outcome, and the type of data available. An ITS design requires the pre- and post-intervention periods to be clearly differentiated. When used prospectively, the investigator therefore needs to have control over the timing of the intervention. ITS analyses typically involve outcomes that are expected to change soon after an intervention is introduced or after a well-defined lag period. For example, for outcomes such as cancer or incident tuberculosis that develop long after an intervention is introduced and at a variable rate, it is difficult to clearly separate the pre- and post-intervention periods. Last, an ITS analysis requires at least three time points in the pre- and post-intervention periods to assess trends. In general, a larger number of time points is recommended, particularly when the expected effect size is smaller, data are more similar at closer together time points ( i.e., auto-correlation), or confounding effects ( e.g., seasonality) are present. It is also important for investigators to consider any changes to data collection or recording over time, particularly if such changes are associated with introduction of the intervention.
In comparison to simple pre-post designs in which the average outcome level is compared between the pre- and post-intervention periods, the key advantage of ITS designs is that they evaluate for intervention effect while accounting for pre-intervention trends. Such trends are common due to factors such as changes in the quality of care, data collection and recording, and population characteristics over time. In addition, ITS designs can increase power by making full use of longitudinal data instead of collapsing all data to single pre- and post-intervention time points. The use of longitudinal data can also be helpful for assessing whether intervention effects are short-lived or sustained over time.
While the basic ITS design has important strengths, the key threat to internal validity is the possibility that factors other than the intervention are affecting the observed changes in outcome level or trend. Changes over time in factors such as the quality of care, data collection and recording, and population characteristics may not be fully accounted for by the pre-intervention trend. Similarly, the pre-intervention time period, particularly when short, may not capture seasonal changes in an outcome.
Detailed reviews have been published of variations on the basic ITS design that can be used to enhance causal inference. In particular, the addition of a control group can be particularly useful for assessing for the presence of seasonal trends and other potential time-varying confounders ( 52 ). Zombre et al ( 52 ) maintained a large number of control number of sites during the extended study period and were able to look at variations in seasonal trends as well as clinic-level characteristics, such as workforce density and sustainability. In addition to including a control group, several analysis phase strategies can be employed to strengthen causal inference including adjustment for time varying confounders and accounting for auto correlation.
Stepped wedge designs (SWDs) involve a sequential roll-out of an intervention to participants (individuals or clusters) over several distinct time periods ( 5 , 7 , 22 , 24 , 29 , 30 , 38 ). SWDs can include cohort designs (with the same individuals in each cluster in the pre and post intervention steps), and repeated cross-sectional designs (with different individuals in each cluster in the pre and post intervention steps) ( 7 ). In the SWD, there is a unidirectional, sequential roll- out of an intervention to clusters (or individuals) that occurs over different time periods. Initially all clusters (or individuals) are unexposed to the intervention, and then at regular intervals, selected clusters cross over (or ‘step’) into a time period where they receive the intervention [ Figure 3 here]. All clusters receive the intervention by the last time interval (although not all individuals within clusters necessarily receive the intervention). Data is collected on all clusters such that they each contribute data during both control and intervention time periods. The order in which clusters receive the intervention can be assigned randomly or using some other approach when randomization is not possible. For example, in settings with geographically remote or difficult-to-access populations, a non-random order can maximize efficiency with respect to logistical considerations.
Illustration of the stepped wedge study design-Intervention Roll-Out Over Time*
* Adapted from Turner et al 2017
The practical and social benefits of the stepped wedge design have been summarized in recent reviews ( 5 , 22 , 24 , 27 , 29 , 36 , 38 , 41 , 42 , 45 , 46 , 51 ). In addition to addressing general concerns with RCTs discussed earlier, advantages of SWDs include the logistical convenience of staggered roll-out of the intervention, which enables a.smaller staff to be distributed across different implementation start times and allows for multi-level interventions to be integrated into practice or ‘real world’ settings (referred to as the feasibility benefit). This benefit also applies to studies of de-implementation, prior to a new approach being introduced. For example, with a staggered roll-out it is possible to build in a transition cohort, such that sites can adjust to the integration of the new intervention, and also allow for a switching over in sites to de-implementing a prior practice. For a specified time period there may be ‘mixed’ or incomplete data, which can be excluded from the data analysis. However, associated with a longer duration of roll-out for practical reasons such as this switching, are associated costs in threats to internal validity, discussed below.
There are several limitations to the SWD. These generally involve consequences of the trade-offs related to having design control for the intervention roll-out, often due to logistical reasons on the one hand, but then having ‘down the road’ threats to internal validity. These roll-out related threats include potential lagged intervention effects for non-acute outcomes; possible fatigue and associated higher drop-out rates of waiting for the cross-over among clusters assigned to receive the intervention later; fidelity losses for key intervention components over time; and potential contamination of later clusters ( 22 ). Another drawback of the SWD is that it involves data assessment at each point when a new cluster receives the intervention, substantially increasing the burden of data collection and costs unless data collection can be automated or uses existing data sources. Because the SWD often has more clusters receiving the intervention towards the end of the intervention period than in previous time periods, there is a potential concern that there can be temporal confounding at this stage. The SWD is also not as suited for evaluating intervention effects on delayed health outcomes (such as chronic disease incidence), and is most appropriate when outcomes that occur relatively soon after each cluster starts receiving the intervention. Finally, as logistical necessity often dictates selecting a design with smaller numbers of clusters, there are relatedly challenges in the statistical analysis. To use standard software, the common recommendation is to have at least 20 to 30 clusters ( 35 ).
Stepped wedge designs can embed improvements that can enhance internal validity, mimicking the strength of RCTs. These generally focus on efforts to either reduce bias or achieve balance in covariates across sites and over time; and/or compensate as much as possible for practical decisions made at the implementation stage, which affect the distribution of the intervention over time and by sites. The most widely used approaches are discussed in order of benefit to internal validity: 1) partial randomization; 2) stratification and matching; 3) embedding data collection at critical points in time, such as with a phasing-in of intervention components, and 4) creating a transition cohort or wash-out period. The most important of these SWD elements is random assignment of clusters as to when they will cross over into the intervention period. As well, utilizing data regarding time-varying covariates/confounders, either to stratify clusters and then randomize within strata (partial randomization) or to match clusters on known covariates in the absence of randomization, are techniques often employed to minimize bias and reduce confounding. Finally, maintaining control over the number and timing of data collection points over the study period can be beneficial in several ways. First, it can allow for data analysis strategies that can incorporate cyclical temporal trends (such as seasonality-mediated risk for the outcome, such as with flu or malaria) or other underlying temporal trends. Second, it can enable phased interventions to be studied for the contribution of different components included in the phases (e.g. passive then active intervention components), or can enable ‘pausing’ time, as when there is a structured wash out or transition cohort created for practical reasons (e.g. one intervention or practice is stopped/de-implemented, and a new one is introduced) (see Figure 4 ).
Illustration of the stepped wedge study design- Summary of Exposed and Unexposed Cluster Time*
Adapted from Hemming 2015
Table 2 provides examples of studies using SWD that have used one or more of the design approaches described above to improve the internal validity of the study. In the study by Killam et al 2010 ( 31 ), a non-randomized SWD was used to evaluate a complex clinic-based intervention for integrating anti-retro viral (ART) treatment into routine antenatal care in Zambia for post-partum women. The design involved matching clinics by size and an inverse roll-out, to balance out the sizes across the four groups. The inverse roll-out involved four strata of clinics, grouped by size with two clinics in each strata. The roll-out was sequenced across these eight clinics, such that one smaller clinics began earlier, with three clinics of increasing size getting the intervention afterwards. This was then followed by a descending order of clinics by size for the remaining roll-out, ending with the smallest clinic. This inverse roll-out enabled the investigators to start with a smaller clinic, to work out the logistical considerations, but then influence the roll-out such as to avoid clustering of smaller or larger clinics in any one step of the intervention.
A second design feature of this study involved the use of a transition cohort or wash-out period (see Figure 4 ) (also used in the Morrison et al 2015 study)( 19 , 37 ). This approach can be used when an existing practice is being replaced with the new intervention, but there is ambiguity as to which group an individual would be assigned to while integration efforts were underway. In the Killam study, the concern was regarding women who might be identified as ART-eligible in the control period but actually enroll into and initiate ART at an antenatal clinic during the intervention period. To account for the ambiguity of this transition period, patients with an initial antenatal visit more than 60 days prior to the date of implementing the ART in the intervention sites were excluded. For analysis of the primary outcome, patients were categorized into three mutually exclusive categories: a referral to ART cohort, an integrated ART in the antenatal clinics cohort, and a transition cohort. It is important to note that the time period for a transition cohort can add considerable time to an intervention roll-out, especially when there is to be a de-implementation of an existing practice that involves a wide range or staff or activities. As well, the exclusion of the data during this phase can reduce the study’s power if not built into the sample size considerations at the design phase.
Morrison et al 2015 ( 37 ) used a randomized cluster design, with additional stratification and randomization within relevant sub-groups to examine a two-part quality improvement intervention focusing on clinician uptake of patient cooling procedures for post-cardiac care in hospital settings (referred to as Targeted Temperature Management). In this study, 32 hospitals were stratified into two groups based on intensive care unit size (< 10 beds vs ≥ 10 beds), and then randomly assigned into four different time periods to receive the intervention. The phased intervention implementation included both passive (generic didactic training components regarding the intervention) and an active (tailored support to site-specific barriers identified in passive phase) components. This study exemplifies some of the best uses of SWD in the context of QI interventions that have either multiple components of for which there may be a passive and active phase, as is often the case with interventions that are layered onto systems change requirements (e.g. electronic records improvements/customization) or relate to sequenced guidelines implementation (as in this example).
Studies using a wait-list partial randomization design are also included in Table 2 ( 24 , 27 , 42 ). These types of studies are well-suited to settings where there is routine enumeration of a cohort based on a specific eligibility criteria, such as enrolment in a health plan or employment group, or from a disease-based registry, such as for diabetes ( 27 , 42 ). It has also been reported that this design can increase efficiency and statistical power in contrast to cluster-based trials, a crucial consideration when the number of participating individuals or groups is small ( 22 ).
The study by Grant et al et al uses a variant of the SWD for which individuals within a setting are enumerated and then randomized to get the intervention. In this example, employees who had previously screened positive for HIV at the company clinic as part of mandatory testing, were invited in random sequence to attend a workplace HIV clinic at a large mining facility in South Africa to initiate a preventive treatment for TB during the years prior to the time when ARTs were more widely available. Individuals contributed follow-up time to the “pre-clinic” phase from the baseline date established for the cohort until the actual date of their first clinic visit, and also to the “post- clinic” phase thereafter. Clinic visits every 6 months were used to identify incident TB events. Because they were looking at reduction in TB incidence among the workers at the mine and not just those in the study, the effect of the intervention (the provision of clinic services) was estimated for the entire study population (incidence rate ratio), irrespective of whether they actually received isoniazid.
We present a decision ‘map’ approach based on a Figure 5 to assist in considering decisions in selecting among QEDs and for which features you can pay particular attention to in the design [ Figure 5 here].
Quasi-Experimental Design Decision-Making Map
First, at the top of the flow diagram ( 1 ), consider if you can have multiple time points you can collect data for in the pre and post intervention periods. Ideally, you will be able to select more than two time points. If you cannot, then multiple sites would allow for a non-equivalent pre-post design. If you can have more than the two time points for the study assessments, you next need to determine if you can include multiple sites ( 2 ). If not, then you can consider a single site point ITS. If you can have multiple sites, you can choose between a SWD and a multiple site ITS based on whether or not you observe the roll-out over multiple time points, (SWD) or if you have only one intervention time point (controlled multiple site ITS)
In a recent article in this journal ( 26 ), the following observation was made that there is an unavoidable trade-off between these two forms of validity such that with a higher control of a study, there is stronger evidence for internal validity but that control may jeopardize some of the external validity of that stronger evidence. Nonetheless, there are design strategies for non-experimental studies that can be undertaken to improve the internal validity while not eliminating considerations of external validity. These are described below across all three study designs.
One of the strengths of QEDs is that they are often employed to examine intervention effects in real world settings and often, for more diverse populations and settings. Consequently, if there is adequate examination of characteristics of participants and setting-related factors it can be possible to interpret findings among critical groups for which there may be no existing evidence of an intervention effect for. For example in the Campus Watch intervention ( 16 ), the investigator over-sampled the Maori indigenous population in order to be able to stratify the results and investigate whether the program was effective for this under-studied group. In the study by Zombré et al ( 52 ) on health care access in Burkina Faso, the authors examined clinic density characteristics to determine its impact on sustainability.
Some of the most important outcomes for examination in these QED studies include whether the intervention was delivered as intended (i.e., fidelity), maintained over the entire study period (i.e., sustainability), and if the outcomes could be specifically examined by this level of fidelity within or across sites. As well, when a complex intervention is related to a policy or guideline shift and implementation requires logistical adjustments (such as phased roll-outs to embed the intervention or to train staff), QEDs more truly mimic real world constraints. As a result, capturing processes of implementation are critical as they can describe important variation in uptake, informing interpretation of the findings for external validity. As described by Prost et al ( 41 ), for example, it is essential to capture what occurs during such phased intervention roll-outs, as with following established guidelines for the development of complex interventions including efforts to define and protocolize activities before their implementation ( 17 , 18 , 28 ). However, QEDs are often conducted by teams with strong interests in adapting the intervention or ‘learning by doing’, which can limit interpretation of findings if not planned into the design. As done in the study by Bailet et al ( 3 ), the investigators refined intervention, based on year 1 data, and then applied in years 2–3, at this later time collecting additional data on training and measurement fidelity. This phasing aspect of implementation generates a tension between protocolizing interventions and adapting them as they go along. When this is the case, additional designs for the intervention roll-out, such as adaptive or hybrid designs can also be considered.
External validity can be improved when the intervention is applied to entire communities, as with some of the community-randomized studies described in Table 2 ( 12 , 21 ). In these cases, the results are closer to the conditions that would apply if the interventions were conducted ‘at scale’, with a large proportion of a population receiving the intervention. In some cases QEDs also afford greater access for some intervention research to be conducted in remote or difficult to reach communities, where the cost and logistical requirements of an RCT may become prohibitive or may require alteration of the intervention or staffing support to levels that would never be feasible in real world application.
Frameworks can be helpful to enhances interpretability of many kinds of studies, including QEDs and can help ensure that information on essential implementation strategies are included in the results ( 44 ). Although several of the case studies summarized in this article included measures that can improve external validity (such as sub-group analysis of which participants were most impacted, process and contextual measures that can affect variation in uptake), none formally employ an implementation framework. Green and Glasgow (2006) ( 25 ) have outlined several useful criteria for gaging the extent to which an evaluation study also provides measures that enhance interpretation of external validity, for which those employing QEDs could identify relevant components and frameworks to include in reported findings.
It has been observed that it is more difficult to conduct a good quasi-experiment than to conduct a good randomized trial ( 43 ). Although QEDs are increasingly used, it is important to note that randomized designs are still preferred over quasi-experiments except where randomization is not possible. In this paper we present three important QEDs and variants nested within them that can increase internal validity while also improving external validity considerations, and present case studies employing these techniques.
1 It is important to note that if such randomization would be possible at the site level based on similar sites, a cluster randomized control trial would be an option.
Guide Title: Experimental and Quasi-Experimental Research Guide ID: 64
You approach a stainless-steel wall, separated vertically along its middle where two halves meet. After looking to the left, you see two buttons on the wall to the right. You press the top button and it lights up. A soft tone sounds and the two halves of the wall slide apart to reveal a small room. You step into the room. Looking to the left, then to the right, you see a panel of more buttons. You know that you seek a room marked with the numbers 1-0-1-2, so you press the button marked "10." The halves slide shut and enclose you within the cubicle, which jolts upward. Soon, the soft tone sounds again. The door opens again. On the far wall, a sign silently proclaims, "10th floor."
You have engaged in a series of experiments. A ride in an elevator may not seem like an experiment, but it, and each step taken towards its ultimate outcome, are common examples of a search for a causal relationship-which is what experimentation is all about.
You started with the hypothesis that this is in fact an elevator. You proved that you were correct. You then hypothesized that the button to summon the elevator was on the left, which was incorrect, so then you hypothesized it was on the right, and you were correct. You hypothesized that pressing the button marked with the up arrow would not only bring an elevator to you, but that it would be an elevator heading in the up direction. You were right.
As this guide explains, the deliberate process of testing hypotheses and reaching conclusions is an extension of commonplace testing of cause and effect relationships.
Discovering causal relationships is the key to experimental research. In abstract terms, this means the relationship between a certain action, X, which alone creates the effect Y. For example, turning the volume knob on your stereo clockwise causes the sound to get louder. In addition, you could observe that turning the knob clockwise alone, and nothing else, caused the sound level to increase. You could further conclude that a causal relationship exists between turning the knob clockwise and an increase in volume; not simply because one caused the other, but because you are certain that nothing else caused the effect.
Beyond discovering causal relationships, experimental research further seeks out how much cause will produce how much effect; in technical terms, how the independent variable will affect the dependent variable. You know that turning the knob clockwise will produce a louder noise, but by varying how much you turn it, you see how much sound is produced. On the other hand, you might find that although you turn the knob a great deal, sound doesn't increase dramatically. Or, you might find that turning the knob just a little adds more sound than expected. The amount that you turned the knob is the independent variable, the variable that the researcher controls, and the amount of sound that resulted from turning it is the dependent variable, the change that is caused by the independent variable.
Experimental research also looks into the effects of removing something. For example, if you remove a loud noise from the room, will the person next to you be able to hear you? Or how much noise needs to be removed before that person can hear you?
The term treatment refers to either removing or adding a stimulus in order to measure an effect (such as turning the knob a little or a lot, or reducing the noise level a little or a lot). Experimental researchers want to know how varying levels of treatment will affect what they are studying. As such, researchers often have an idea, or hypothesis, about what effect will occur when they cause something. Few experiments are performed where there is no idea of what will happen. From past experiences in life or from the knowledge we possess in our specific field of study, we know how some actions cause other reactions. Experiments confirm or reconfirm this fact.
Experimentation becomes more complex when the causal relationships they seek aren't as clear as in the stereo knob-turning examples. Questions like "Will olestra cause cancer?" or "Will this new fertilizer help this plant grow better?" present more to consider. For example, any number of things could affect the growth rate of a plant-the temperature, how much water or sun it receives, or how much carbon dioxide is in the air. These variables can affect an experiment's results. An experimenter who wants to show that adding a certain fertilizer will help a plant grow better must ensure that it is the fertilizer, and nothing else, affecting the growth patterns of the plant. To do this, as many of these variables as possible must be controlled.
In the example used in this guide (you'll find the example below), we discuss an experiment that focuses on three groups of plants -- one that is treated with a fertilizer named MegaGro, another group treated with a fertilizer named Plant!, and yet another that is not treated with fetilizer (this latter group serves as a "control" group). In this example, even though the designers of the experiment have tried to remove all extraneous variables, results may appear merely coincidental. Since the goal of the experiment is to prove a causal relationship in which a single variable is responsible for the effect produced, the experiment would produce stronger proof if the results were replicated in larger treatment and control groups.
Selecting groups entails assigning subjects in the groups of an experiment in such a way that treatment and control groups are comparable in all respects except the application of the treatment. Groups can be created in two ways: matching and randomization. In the MegaGro experiment discussed below, the plants might be matched according to characteristics such as age, weight and whether they are blooming. This involves distributing these plants so that each plant in one group exactly matches characteristics of plants in the other groups. Matching may be problematic, though, because it "can promote a false sense of security by leading [the experimenter] to believe that [the] experimental and control groups were really equated at the outset, when in fact they were not equated on a host of variables" (Jones, 291). In other words, you may have flowers for your MegaGro experiment that you matched and distributed among groups, but other variables are unaccounted for. It would be difficult to have equal groupings.
Randomization, then, is preferred to matching. This method is based on the statistical principle of normal distribution. Theoretically, any arbitrarily selected group of adequate size will reflect normal distribution. Differences between groups will average out and become more comparable. The principle of normal distribution states that in a population most individuals will fall within the middle range of values for a given characteristic, with increasingly fewer toward either extreme (graphically represented as the ubiquitous "bell curve").
Thus far, we have explained that for experimental research we need:
But what if we don't have all of those? Do we still have an experiment? Not a true experiment in the strictest scientific sense of the term, but we can have a quasi-experiment, an attempt to uncover a causal relationship, even though the researcher cannot control all the factors that might affect the outcome.
A quasi-experimenter treats a given situation as an experiment even though it is not wholly by design. The independent variable may not be manipulated by the researcher, treatment and control groups may not be randomized or matched, or there may be no control group. The researcher is limited in what he or she can say conclusively.
The significant element of both experiments and quasi-experiments is the measure of the dependent variable, which it allows for comparison. Some data is quite straightforward, but other measures, such as level of self-confidence in writing ability, increase in creativity or in reading comprehension are inescapably subjective. In such cases, quasi-experimentation often involves a number of strategies to compare subjectivity, such as rating data, testing, surveying, and content analysis.
Rating essentially is developing a rating scale to evaluate data. In testing, experimenters and quasi-experimenters use ANOVA (Analysis of Variance) and ANCOVA (Analysis of Co-Variance) tests to measure differences between control and experimental groups, as well as different correlations between groups.
Since we're mentioning the subject of statistics, note that experimental or quasi-experimental research cannot state beyond a shadow of a doubt that a single cause will always produce any one effect. They can do no more than show a probability that one thing causes another. The probability that a result is the due to random chance is an important measure of statistical analysis and in experimental research.
Example: Causality
Let's say you want to determine that your new fertilizer, MegaGro, will increase the growth rate of plants. You begin by getting a plant to go with your fertilizer. Since the experiment is concerned with proving that MegaGro works, you need another plant, using no fertilizer at all on it, to compare how much change your fertilized plant displays. This is what is known as a control group.
Set up with a control group, which will receive no treatment, and an experimental group, which will get MegaGro, you must then address those variables that could invalidate your experiment. This can be an extensive and exhaustive process. You must ensure that you use the same plant; that both groups are put in the same kind of soil; that they receive equal amounts of water and sun; that they receive the same amount of exposure to carbon-dioxide-exhaling researchers, and so on. In short, any other variable that might affect the growth of those plants, other than the fertilizer, must be the same for both plants. Otherwise, you can't prove absolutely that MegaGro is the only explanation for the increased growth of one of those plants.
Such an experiment can be done on more than two groups. You may not only want to show that MegaGro is an effective fertilizer, but that it is better than its competitor brand of fertilizer, Plant! All you need to do, then, is have one experimental group receiving MegaGro, one receiving Plant! and the other (the control group) receiving no fertilizer. Those are the only variables that can be different between the three groups; all other variables must be the same for the experiment to be valid.
Controlling variables allows the researcher to identify conditions that may affect the experiment's outcome. This may lead to alternative explanations that the researcher is willing to entertain in order to isolate only variables judged significant. In the MegaGro experiment, you may be concerned with how fertile the soil is, but not with the plants'; relative position in the window, as you don't think that the amount of shade they get will affect their growth rate. But what if it did? You would have to go about eliminating variables in order to determine which is the key factor. What if one receives more shade than the other and the MegaGro plant, which received more shade, died? This might prompt you to formulate a plausible alternative explanation, which is a way of accounting for a result that differs from what you expected. You would then want to redo the study with equal amounts of sunlight.
Experimental research can be roughly divided into five phases:
The process starts by clearly identifying the problem you want to study and considering what possible methods will affect a solution. Then you choose the method you want to test, and formulate a hypothesis to predict the outcome of the test.
For example, you may want to improve student essays, but you don't believe that teacher feedback is enough. You hypothesize that some possible methods for writing improvement include peer workshopping, or reading more example essays. Favoring the former, your experiment would try to determine if peer workshopping improves writing in high school seniors. You state your hypothesis: peer workshopping prior to turning in a final draft will improve the quality of the student's essay.
The next step is to devise an experiment to test your hypothesis. In doing so, you must consider several factors. For example, how generalizable do you want your end results to be? Do you want to generalize about the entire population of high school seniors everywhere, or just the particular population of seniors at your specific school? This will determine how simple or complex the experiment will be. The amount of time funding you have will also determine the size of your experiment.
Continuing the example from step one, you may want a small study at one school involving three teachers, each teaching two sections of the same course. The treatment in this experiment is peer workshopping. Each of the three teachers will assign the same essay assignment to both classes; the treatment group will participate in peer workshopping, while the control group will receive only teacher comments on their drafts.
At the start of an experiment, the control and treatment groups must be selected. Whereas the "hard" sciences have the luxury of attempting to create truly equal groups, educators often find themselves forced to conduct their experiments based on self-selected groups, rather than on randomization. As was highlighted in the Basic Concepts section, this makes the study a quasi-experiment, since the researchers cannot control all of the variables.
For the peer workshopping experiment, let's say that it involves six classes and three teachers with a sample of students randomly selected from all the classes. Each teacher will have a class for a control group and a class for a treatment group. The essay assignment is given and the teachers are briefed not to change any of their teaching methods other than the use of peer workshopping. You may see here that this is an effort to control a possible variable: teaching style variance.
The fourth step is to collect and analyze the data. This is not solely a step where you collect the papers, read them, and say your methods were a success. You must show how successful. You must devise a scale by which you will evaluate the data you receive, therefore you must decide what indicators will be, and will not be, important.
Continuing our example, the teachers' grades are first recorded, then the essays are evaluated for a change in sentence complexity, syntactical and grammatical errors, and overall length. Any statistical analysis is done at this time if you choose to do any. Notice here that the researcher has made judgments on what signals improved writing. It is not simply a matter of improved teacher grades, but a matter of what the researcher believes constitutes improved use of the language.
Once you have completed the experiment, you will want to share findings by publishing academic paper (or presentations). These papers usually have the following format, but it is not necessary to follow it strictly. Sections can be combined or not included, depending on the structure of the experiment, and the journal to which you submit your paper.
Several issues are addressed in this section, including the use of experimental and quasi-experimental research in educational settings, the relevance of the methods to English studies, and ethical concerns regarding the methods.
Charting causal relationships in human settings.
Any time a human population is involved, prediction of casual relationships becomes cloudy and, some say, impossible. Many reasons exist for this; for example,
But such confounding variables don't stop researchers from trying to identify causal relationships in education. Educators naturally experiment anyway, comparing groups, assessing the attributes of each, and making predictions based on an evaluation of alternatives. They look to research to support their intuitive practices, experimenting whenever they try to decide which instruction method will best encourage student improvement.
The goal of educational research lies in combining theory, research, and practice. Educational researchers attempt to establish models of teaching practice, learning styles, curriculum development, and countless other educational issues. The aim is to "try to improve our understanding of education and to strive to find ways to have understanding contribute to the improvement of practice," one writer asserts (Floden 1996, p. 197).
In quasi-experimentation, researchers try to develop models by involving teachers as researchers, employing observational research techniques. Although results of this kind of research are context-dependent and difficult to generalize, they can act as a starting point for further study. The "educational researcher . . . provides guidelines and interpretive material intended to liberate the teacher's intelligence so that whatever artistry in teaching the teacher can achieve will be employed" (Eisner 1992, p. 8).
Critics contend that the educational researcher is inherently biased, sample selection is arbitrary, and replication is impossible. The key to combating such criticism has to do with rigor. Rigor is established through close, proper attention to randomizing groups, time spent on a study, and questioning techniques. This allows more effective application of standards of quantitative research to qualitative research.
Often, teachers cannot wait to for piles of experimentation data to be analyzed before using the teaching methods (Lauer and Asher 1988). They ultimately must assess whether the results of a study in a distant classroom are applicable in their own classrooms. And they must continuously test the effectiveness of their methods by using experimental and qualitative research simultaneously. In addition to statistics (quantitative), researchers may perform case studies or observational research (qualitative) in conjunction with, or prior to, experimentation.
Situations in english studies that might encourage use of experimental methods.
Whenever a researcher would like to see if a causal relationship exists between groups, experimental and quasi-experimental research can be a viable research tool. Researchers in English Studies might use experimentation when they believe a relationship exists between two variables, and they want to show that these two variables have a significant correlation (or causal relationship).
A benefit of experimentation is the ability to control variables, such as the amount of treatment, when it is given, to whom and so forth. Controlling variables allows researchers to gain insight into the relationships they believe exist. For example, a researcher has an idea that writing under pseudonyms encourages student participation in newsgroups. Researchers can control which students write under pseudonyms and which do not, then measure the outcomes. Researchers can then analyze results and determine if this particular variable alone causes increased participation.
Experimentation and quasi-experimentation allow for generating transferable results and accepting those results as being dependent upon experimental rigor. It is an effective alternative to generalizability, which is difficult to rely upon in educational research. English scholars, reading results of experiments with a critical eye, ultimately decide if results will be implemented and how. They may even extend that existing research by replicating experiments in the interest of generating new results and benefiting from multiple perspectives. These results will strengthen the study or discredit findings.
Researchers should carefully consider if a particular method is feasible in humanities studies, and whether it will yield the desired information. Some researchers recommend addressing pertinent issues combining several research methods, such as survey, interview, ethnography, case study, content analysis, and experimentation (Lauer and Asher, 1988).
In educational research, experimentation is a way to gain insight into methods of instruction. Although teaching is context specific, results can provide a starting point for further study. Often, a teacher/researcher will have a "gut" feeling about an issue which can be explored through experimentation and looking at causal relationships. Through research intuition can shape practice .
A preconception exists that information obtained through scientific method is free of human inconsistencies. But, since scientific method is a matter of human construction, it is subject to human error . The researcher's personal bias may intrude upon the experiment , as well. For example, certain preconceptions may dictate the course of the research and affect the behavior of the subjects. The issue may be compounded when, although many researchers are aware of the affect that their personal bias exerts on their own research, they are pressured to produce research that is accepted in their field of study as "legitimate" experimental research.
The researcher does bring bias to experimentation, but bias does not limit an ability to be reflective . An ethical researcher thinks critically about results and reports those results after careful reflection. Concerns over bias can be leveled against any research method.
Often, the sample may not be representative of a population, because the researcher does not have an opportunity to ensure a representative sample. For example, subjects could be limited to one location, limited in number, studied under constrained conditions and for too short a time.
Despite such inconsistencies in educational research, the researcher has control over the variables , increasing the possibility of more precisely determining individual effects of each variable. Also, determining interaction between variables is more possible.
Even so, artificial results may result . It can be argued that variables are manipulated so the experiment measures what researchers want to examine; therefore, the results are merely contrived products and have no bearing in material reality. Artificial results are difficult to apply in practical situations, making generalizing from the results of a controlled study questionable. Experimental research essentially first decontextualizes a single question from a "real world" scenario, studies it under controlled conditions, and then tries to recontextualize the results back on the "real world" scenario. Results may be difficult to replicate .
Perhaps, groups in an experiment may not be comparable . Quasi-experimentation in educational research is widespread because not only are many researchers also teachers, but many subjects are also students. With the classroom as laboratory, it is difficult to implement randomizing or matching strategies. Often, students self-select into certain sections of a course on the basis of their own agendas and scheduling needs. Thus when, as often happens, one class is treated and the other used for a control, the groups may not actually be comparable. As one might imagine, people who register for a class which meets three times a week at eleven o'clock in the morning (young, no full-time job, night people) differ significantly from those who register for one on Monday evenings from seven to ten p.m. (older, full-time job, possibly more highly motivated). Each situation presents different variables and your group might be completely different from that in the study. Long-term studies are expensive and hard to reproduce. And although often the same hypotheses are tested by different researchers, various factors complicate attempts to compare or synthesize them. It is nearly impossible to be as rigorous as the natural sciences model dictates.
Even when randomization of students is possible, problems arise. First, depending on the class size and the number of classes, the sample may be too small for the extraneous variables to cancel out. Second, the study population is not strictly a sample, because the population of students registered for a given class at a particular university is obviously not representative of the population of all students at large. For example, students at a suburban private liberal-arts college are typically young, white, and upper-middle class. In contrast, students at an urban community college tend to be older, poorer, and members of a racial minority. The differences can be construed as confounding variables: the first group may have fewer demands on its time, have less self-discipline, and benefit from superior secondary education. The second may have more demands, including a job and/or children, have more self-discipline, but an inferior secondary education. Selecting a population of subjects which is representative of the average of all post-secondary students is also a flawed solution, because the outcome of a treatment involving this group is not necessarily transferable to either the students at a community college or the students at the private college, nor are they universally generalizable.
When a human population is involved, experimental research becomes concerned if behavior can be predicted or studied with validity. Human response can be difficult to measure . Human behavior is dependent on individual responses. Rationalizing behavior through experimentation does not account for the process of thought, making outcomes of that process fallible (Eisenberg, 1996).
Nevertheless, we perform experiments daily anyway . When we brush our teeth every morning, we are experimenting to see if this behavior will result in fewer cavities. We are relying on previous experimentation and we are transferring the experimentation to our daily lives.
Moreover, experimentation can be combined with other research methods to ensure rigor . Other qualitative methods such as case study, ethnography, observational research and interviews can function as preconditions for experimentation or conducted simultaneously to add validity to a study.
We have few alternatives to experimentation. Mere anecdotal research , for example is unscientific, unreplicatable, and easily manipulated. Should we rely on Ed walking into a faculty meeting and telling the story of Sally? Sally screamed, "I love writing!" ten times before she wrote her essay and produced a quality paper. Therefore, all the other faculty members should hear this anecdote and know that all other students should employ this similar technique.
On final disadvantage: frequently, political pressure drives experimentation and forces unreliable results. Specific funding and support may drive the outcomes of experimentation and cause the results to be skewed. The reader of these results may not be aware of these biases and should approach experimentation with a critical eye.
Experimental and quasi-experimental research can be summarized in terms of their advantages and disadvantages. This section combines and elaborates upon many points mentioned previously in this guide.
|
|
gain insight into methods of instruction | subject to human error |
intuitive practice shaped by research | personal bias of researcher may intrude |
teachers have bias but can be reflective | sample may not be representative |
researcher can have control over variables | can produce artificial results |
humans perform experiments anyway | results may only apply to one situation and may be difficult to replicate |
can be combined with other research methods for rigor | groups may not be comparable |
use to determine what is best for population | human response can be difficult to measure |
provides for greater transferability than anecdotal research | political pressure may skew results |
Experimental research may be manipulated on both ends of the spectrum: by researcher and by reader. Researchers who report on experimental research, faced with naive readers of experimental research, encounter ethical concerns. While they are creating an experiment, certain objectives and intended uses of the results might drive and skew it. Looking for specific results, they may ask questions and look at data that support only desired conclusions. Conflicting research findings are ignored as a result. Similarly, researchers, seeking support for a particular plan, look only at findings which support that goal, dismissing conflicting research.
Editors and journals do not publish only trouble-free material. As readers of experiments members of the press might report selected and isolated parts of a study to the public, essentially transferring that data to the general population which may not have been intended by the researcher. Take, for example, oat bran. A few years ago, the press reported how oat bran reduces high blood pressure by reducing cholesterol. But that bit of information was taken out of context. The actual study found that when people ate more oat bran, they reduced their intake of saturated fats high in cholesterol. People started eating oat bran muffins by the ton, assuming a causal relationship when in actuality a number of confounding variables might influence the causal link.
Ultimately, ethical use and reportage of experimentation should be addressed by researchers, reporters and readers alike.
Reporters of experimental research often seek to recognize their audience's level of knowledge and try not to mislead readers. And readers must rely on the author's skill and integrity to point out errors and limitations. The relationship between researcher and reader may not sound like a problem, but after spending months or years on a project to produce no significant results, it may be tempting to manipulate the data to show significant results in order to jockey for grants and tenure.
Meanwhile, the reader may uncritically accept results that receive validity by being published in a journal. However, research that lacks credibility often is not published; consequentially, researchers who fail to publish run the risk of being denied grants, promotions, jobs, and tenure. While few researchers are anything but earnest in their attempts to conduct well-designed experiments and present the results in good faith, rhetorical considerations often dictate a certain minimization of methodological flaws.
Concerns arise if researchers do not report all, or otherwise alter, results. This phenomenon is counterbalanced, however, in that professionals are also rewarded for publishing critiques of others' work. Because the author of an experimental study is in essence making an argument for the existence of a causal relationship, he or she must be concerned not only with its integrity, but also with its presentation. Achieving persuasiveness in any kind of writing involves several elements: choosing a topic of interest, providing convincing evidence for one's argument, using tone and voice to project credibility, and organizing the material in a way that meets expectations for a logical sequence. Of course, what is regarded as pertinent, accepted as evidence, required for credibility, and understood as logical varies according to context. If the experimental researcher hopes to make an impact on the community of professionals in their field, she must attend to the standards and orthodoxy's of that audience.
Contrasts: Traditional and computer-supported writing classrooms. This Web presents a discussion of the Transitions Study, a year-long exploration of teachers and students in computer-supported and traditional writing classrooms. Includes description of study, rationale for conducting the study, results and implications of the study.
http://kairos.technorhetoric.net/2.2/features/reflections/page1.htm
A cozy world of trivial pursuits? (1996, June 28) The Times Educational Supplement . 4174, pp. 14-15.
A critique discounting the current methods Great Britain employs to fund and disseminate educational research. The belief is that research is performed for fellow researchers not the teaching public and implications for day to day practice are never addressed.
Anderson, J. A. (1979, Nov. 10-13). Research as argument: the experimental form. Paper presented at the annual meeting of the Speech Communication Association, San Antonio, TX.
In this paper, the scientist who uses the experimental form does so in order to explain that which is verified through prediction.
Anderson, Linda M. (1979). Classroom-based experimental studies of teaching effectiveness in elementary schools . (Technical Report UTR&D-R- 4102). Austin: Research and Development Center for Teacher Education, University of Texas.
Three recent large-scale experimental studies have built on a database established through several correlational studies of teaching effectiveness in elementary school.
Asher, J. W. (1976). Educational research and evaluation methods . Boston: Little, Brown.
Abstract unavailable by press time.
Babbie, Earl R. (1979). The Practice of Social Research . Belmont, CA: Wadsworth.
A textbook containing discussions of several research methodologies used in social science research.
Bangert-Drowns, R.L. (1993). The word processor as instructional tool: a meta-analysis of word processing in writing instruction. Review of Educational Research, 63 (1), 69-93.
Beach, R. (1993). The effects of between-draft teacher evaluation versus student self-evaluation on high school students' revising of rough drafts. Research in the Teaching of English, 13 , 111-119.
The question of whether teacher evaluation or guided self-evaluation of rough drafts results in increased revision was addressed in Beach's study. Differences in the effects of teacher evaluations, guided self-evaluation (using prepared guidelines,) and no evaluation of rough drafts were examined. The final drafts of students (10th, 11th, and 12th graders) were compared with their rough drafts and rated by judges according to degree of change.
Beishuizen, J. & Moonen, J. (1992). Research in technology enriched schools: a case for cooperation between teachers and researchers . (ERIC Technical Report ED351006).
This paper describes the research strategies employed in the Dutch Technology Enriched Schools project to encourage extensive and intensive use of computers in a small number of secondary schools, and to study the effects of computer use on the classroom, the curriculum, and school administration and management.
Borg, W. P. (1989). Educational Research: an Introduction . (5th ed.). New York: Longman.
An overview of educational research methodology, including literature review and discussion of approaches to research, experimental design, statistical analysis, ethics, and rhetorical presentation of research findings.
Campbell, D. T., & Stanley, J. C. (1963). Experimental and quasi-experimental designs for research . Boston: Houghton Mifflin.
A classic overview of research designs.
Campbell, D.T. (1988). Methodology and epistemology for social science: selected papers . ed. E. S. Overman. Chicago: University of Chicago Press.
This is an overview of Campbell's 40-year career and his work. It covers in seven parts measurement, experimental design, applied social experimentation, interpretive social science, epistemology and sociology of science. Includes an extensive bibliography.
Caporaso, J. A., & Roos, Jr., L. L. (Eds.). Quasi-experimental approaches: Testing theory and evaluating policy. Evanston, WA: Northwestern University Press.
A collection of articles concerned with explicating the underlying assumptions of quasi-experimentation and relating these to true experimentation. With an emphasis on design. Includes a glossary of terms.
Collier, R. Writing and the word processor: How wary of the gift-giver should we be? Unpublished manuscript.
Unpublished typescript. Charts the developments to date in computers and composition and speculates about the future within the framework of Willie Sypher's model of the evolution of creative discovery.
Cook, T.D. & Campbell, D.T. (1979). Quasi-experimentation: design and analysis issues for field settings . Boston: Houghton Mifflin Co.
The authors write that this book "presents some quasi-experimental designs and design features that can be used in many social research settings. The designs serve to probe causal hypotheses about a wide variety of substantive issues in both basic and applied research."
Cutler, A. (1970). An experimental method for semantic field study. Linguistic Communication, 2 , N. pag.
This paper emphasizes the need for empirical research and objective discovery procedures in semantics, and illustrates a method by which these goals may be obtained.
Daniels, L. B. (1996, Summer). Eisenberg's Heisenberg: The indeterminancies of rationality. Curriculum Inquiry, 26 , 181-92.
Places Eisenberg's theories in relation to the death of foundationalism by showing that he distorts rational studies into a form of relativism. He looks at Eisenberg's ideas on indeterminacy, methods and evidence, what he is against and what we should think of what he says.
Danziger, K. (1990). Constructing the subject: Historical origins of psychological research. Cambridge: Cambridge University Press.
Danzinger stresses the importance of being aware of the framework in which research operates and of the essentially social nature of scientific activity.
Diener, E., et al. (1972, December). Leakage of experimental information to potential future subjects by debriefed subjects. Journal of Experimental Research in Personality , 264-67.
Research regarding research: an investigation of the effects on the outcome of an experiment in which information about the experiment had been leaked to subjects. The study concludes that such leakage is not a significant problem.
Dudley-Marling, C., & Rhodes, L. K. (1989). Reflecting on a close encounter with experimental research. Canadian Journal of English Language Arts. 12 , 24-28.
Researchers, Dudley-Marling and Rhodes, address some problems they met in their experimental approach to a study of reading comprehension. This article discusses the limitations of experimental research, and presents an alternative to experimental or quantitative research.
Edgington, E. S. (1985). Random assignment and experimental research. Educational Administration Quarterly, 21 , N. pag.
Edgington explores ways on which random assignment can be a part of field studies. The author discusses both non-experimental and experimental research and the need for using random assignment.
Eisenberg, J. (1996, Summer). Response to critiques by R. Floden, J. Zeuli, and L. Daniels. Curriculum Inquiry, 26 , 199-201.
A response to critiques of his argument that rational educational research methods are at best suspect and at worst futile. He believes indeterminacy controls this method and worries that chaotic research is failing students.
Eisner, E. (1992, July). Are all causal claims positivistic? A reply to Francis Schrag. Educational Researcher, 21 (5), 8-9.
Eisner responds to Schrag who claimed that critics like Eisner cannot escape a positivistic paradigm whatever attempts they make to do so. Eisner argues that Schrag essentially misses the point for trying to argue for the paradigm solely on the basis of cause and effect without including the rest of positivistic philosophy. This weakens his argument against multiple modal methods, which Eisner argues provides opportunities to apply the appropriate research design where it is most applicable.
Floden, R.E. (1996, Summer). Educational research: limited, but worthwhile and maybe a bargain. (response to J.A. Eisenberg). Curriculum Inquiry, 26 , 193-7.
Responds to John Eisenberg critique of educational research by asserting the connection between improvement of practice and research results. He places high value of teacher discrepancy and knowledge that research informs practice.
Fortune, J. C., & Hutson, B. A. (1994, March/April). Selecting models for measuring change when true experimental conditions do not exist. Journal of Educational Research, 197-206.
This article reviews methods for minimizing the effects of nonideal experimental conditions by optimally organizing models for the measurement of change.
Fox, R. F. (1980). Treatment of writing apprehension and tts effects on composition. Research in the Teaching of English, 14 , 39-49.
The main purpose of Fox's study was to investigate the effects of two methods of teaching writing on writing apprehension among entry level composition students, A conventional teaching procedure was used with a control group, while a workshop method was employed with the treatment group.
Gadamer, H-G. (1976). Philosophical hermeneutics . (D. E. Linge, Trans.). Berkeley, CA: University of California Press.
A collection of essays with the common themes of the mediation of experience through language, the impossibility of objectivity, and the importance of context in interpretation.
Gaise, S. J. (1981). Experimental vs. non-experimental research on classroom second language learning. Bilingual Education Paper Series, 5 , N. pag.
Aims on classroom-centered research on second language learning and teaching are considered and contrasted with the experimental approach.
Giordano, G. (1983). Commentary: Is experimental research snowing us? Journal of Reading, 27 , 5-7.
Do educational research findings actually benefit teachers and students? Giordano states his opinion that research may be helpful to teaching, but is not essential and often is unnecessary.
Goldenson, D. R. (1978, March). An alternative view about the role of the secondary school in political socialization: A field-experimental study of theory and research in social education. Theory and Research in Social Education , 44-72.
This study concludes that when political discussion among experimental groups of secondary school students is led by a teacher, the degree to which the students' views were impacted is proportional to the credibility of the teacher.
Grossman, J., and J. P. Tierney. (1993, October). The fallibility of comparison groups. Evaluation Review , 556-71.
Grossman and Tierney present evidence to suggest that comparison groups are not the same as nontreatment groups.
Harnisch, D. L. (1992). Human judgment and the logic of evidence: A critical examination of research methods in special education transition literature. In D. L. Harnisch et al. (Eds.), Selected readings in transition.
This chapter describes several common types of research studies in special education transition literature and the threats to their validity.
Hawisher, G. E. (1989). Research and recommendations for computers and composition. In G. Hawisher and C. Selfe. (Eds.), Critical Perspectives on Computers and Composition Instruction . (pp. 44-69). New York: Teacher's College Press.
An overview of research in computers and composition to date. Includes a synthesis grid of experimental research.
Hillocks, G. Jr. (1982). The interaction of instruction, teacher comment, and revision in teaching the composing process. Research in the Teaching of English, 16 , 261-278.
Hillock conducted a study using three treatments: observational or data collecting activities prior to writing, use of revisions or absence of same, and either brief or lengthy teacher comments to identify effective methods of teaching composition to seventh and eighth graders.
Jenkinson, J. C. (1989). Research design in the experimental study of intellectual disability. International Journal of Disability, Development, and Education, 69-84.
This article catalogues the difficulties of conducting experimental research where the subjects are intellectually disables and suggests alternative research strategies.
Jones, R. A. (1985). Research Methods in the Social and Behavioral Sciences. Sunderland, MA: Sinauer Associates, Inc..
A textbook designed to provide an overview of research strategies in the social sciences, including survey, content analysis, ethnographic approaches, and experimentation. The author emphasizes the importance of applying strategies appropriately and in variety.
Kamil, M. L., Langer, J. A., & Shanahan, T. (1985). Understanding research in reading and writing . Newton, Massachusetts: Allyn and Bacon.
Examines a wide variety of problems in reading and writing, with a broad range of techniques, from different perspectives.
Kennedy, J. L. (1985). An Introduction to the Design and Analysis of Experiments in Behavioral Research . Lanham, MD: University Press of America.
An introductory textbook of psychological and educational research.
Keppel, G. (1991). Design and analysis: a researcher's handbook . Englewood Cliffs, NJ: Prentice Hall.
This updates Keppel's earlier book subtitled "a student's handbook." Focuses on extensive information about analytical research and gives a basic picture of research in psychology. Covers a range of statistical topics. Includes a subject and name index, as well as a glossary.
Knowles, G., Elija, R., & Broadwater, K. (1996, Spring/Summer). Teacher research: enhancing the preparation of teachers? Teaching Education, 8 , 123-31.
Researchers looked at one teacher candidate who participated in a class which designed their own research project correlating to a question they would like answered in the teaching world. The goal of the study was to see if preservice teachers developed reflective practice by researching appropriate classroom contexts.
Lace, J., & De Corte, E. (1986, April 16-20). Research on media in western Europe: A myth of sisyphus? Paper presented at the annual meeting of the American Educational Research Association. San Francisco.
Identifies main trends in media research in western Europe, with emphasis on three successive stages since 1960: tools technology, systems technology, and reflective technology.
Latta, A. (1996, Spring/Summer). Teacher as researcher: selected resources. Teaching Education, 8 , 155-60.
An annotated bibliography on educational research including milestones of thought, practical applications, successful outcomes, seminal works, and immediate practical applications.
Lauer. J.M. & Asher, J. W. (1988). Composition research: Empirical designs . New York: Oxford University Press.
Approaching experimentation from a humanist's perspective to it, authors focus on eight major research designs: Case studies, ethnographies, sampling and surveys, quantitative descriptive studies, measurement, true experiments, quasi-experiments, meta-analyses, and program evaluations. It takes on the challenge of bridging language of social science with that of the humanist. Includes name and subject indexes, as well as a glossary and a glossary of symbols.
Mishler, E. G. (1979). Meaning in context: Is there any other kind? Harvard Educational Review, 49 , 1-19.
Contextual importance has been largely ignored by traditional research approaches in social/behavioral sciences and in their application to the education field. Developmental and social psychologists have increasingly noted the inadequacies of this approach. Drawing examples for phenomenology, sociolinguistics, and ethnomethodology, the author proposes alternative approaches for studying meaning in context.
Mitroff, I., & Bonoma, T. V. (1978, May). Psychological assumptions, experimentations, and real world problems: A critique and an alternate approach to evaluation. Evaluation Quarterly , 235-60.
The authors advance the notion of dialectic as a means to clarify and examine the underlying assumptions of experimental research methodology, both in highly controlled situations and in social evaluation.
Muller, E. W. (1985). Application of experimental and quasi-experimental research designs to educational software evaluation. Educational Technology, 25 , 27-31.
Muller proposes a set of guidelines for the use of experimental and quasi-experimental methods of research in evaluating educational software. By obtaining empirical evidence of student performance, it is possible to evaluate if programs are making the desired learning effect.
Murray, S., et al. (1979, April 8-12). Technical issues as threats to internal validity of experimental and quasi-experimental designs . San Francisco: University of California.
The article reviews three evaluation models and analyzes the flaws common to them. Remedies are suggested.
Muter, P., & Maurutto, P. (1991). Reading and skimming from computer screens and books: The paperless office revisited? Behavior and Information Technology, 10 (4), 257-66.
The researchers test for reading and skimming effectiveness, defined as accuracy combined with speed, for written text compared to text on a computer monitor. They conclude that, given optimal on-line conditions, both are equally effective.
O'Donnell, A., Et al. (1992). The impact of cooperative writing. In J. R. Hayes, et al. (Eds.). Reading empirical research studies: The rhetoric of research . (pp. 371-84). Hillsdale, NJ: Lawrence Erlbaum Associates.
A model of experimental design. The authors investigate the efficacy of cooperative writing strategies, as well as the transferability of skills learned to other, individual writing situations.
Palmer, D. (1988). Looking at philosophy . Mountain View, CA: Mayfield Publishing.
An introductory text with incisive but understandable discussions of the major movements and thinkers in philosophy from the Pre-Socratics through Sartre. With illustrations by the author. Includes a glossary.
Phelps-Gunn, T., & Phelps-Terasaki, D. (1982). Written language instruction: Theory and remediation . London: Aspen Systems Corporation.
The lack of research in written expression is addressed and an application on the Total Writing Process Model is presented.
Poetter, T. (1996, Spring/Summer). From resistance to excitement: becoming qualitative researchers and reflective practitioners. Teaching Education , 8109-19.
An education professor reveals his own problematic research when he attempted to institute a educational research component to a teacher preparation program. He encountered dissent from students and cooperating professionals and ultimately was rewarded with excitement towards research and a recognized correlation to practice.
Purves, A. C. (1992). Reflections on research and assessment in written composition. Research in the Teaching of English, 26 .
Three issues concerning research and assessment is writing are discussed: 1) School writing is a matter of products not process, 2) school writing is an ill-defined domain, 3) the quality of school writing is what observers report they see. Purves discusses these issues while looking at data collected in a ten-year study of achievement in written composition in fourteen countries.
Rathus, S. A. (1987). Psychology . (3rd ed.). Poughkeepsie, NY: Holt, Rinehart, and Winston.
An introductory psychology textbook. Includes overviews of the major movements in psychology, discussions of prominent examples of experimental research, and a basic explanation of relevant physiological factors. With chapter summaries.
Reiser, R. A. (1982). Improving the research skills of instructional designers. Educational Technology, 22 , 19-21.
In his paper, Reiser starts by stating the importance of research in advancing the field of education, and points out that graduate students in instructional design lack the proper skills to conduct research. The paper then goes on to outline the practicum in the Instructional Systems Program at Florida State University which includes: 1) Planning and conducting an experimental research study; 2) writing the manuscript describing the study; 3) giving an oral presentation in which they describe their research findings.
Report on education research . (Journal). Washington, DC: Capitol Publication, Education News Services Division.
This is an independent bi-weekly newsletter on research in education and learning. It has been publishing since Sept. 1969.
Rossell, C. H. (1986). Why is bilingual education research so bad?: Critique of the Walsh and Carballo study of Massachusetts bilingual education programs . Boston: Center for Applied Social Science, Boston University. (ERIC Working Paper 86-5).
The Walsh and Carballo evaluation of the effectiveness of transitional bilingual education programs in five Massachusetts communities has five flaws and the five flaws are discussed in detail.
Rubin, D. L., & Greene, K. (1992). Gender-typical style in written language. Research in the Teaching of English, 26.
This study was designed to find out whether the writing styles of men and women differ. Rubin and Green discuss the pre-suppositions that women are better writers than men.
Sawin, E. (1992). Reaction: Experimental research in the context of other methods. School of Education Review, 4 , 18-21.
Sawin responds to Gage's article on methodologies and issues in educational research. He agrees with most of the article but suggests the concept of scientific should not be regarded in absolute terms and recommends more emphasis on scientific method. He also questions the value of experiments over other types of research.
Schoonmaker, W. E. (1984). Improving classroom instruction: A model for experimental research. The Technology Teacher, 44, 24-25.
The model outlined in this article tries to bridge the gap between classroom practice and laboratory research, using what Schoonmaker calls active research. Research is conducted in the classroom with the students and is used to determine which two methods of classroom instruction chosen by the teacher is more effective.
Schrag, F. (1992). In defense of positivist research paradigms. Educational Researcher, 21, (5), 5-8.
The controversial defense of the use of positivistic research methods to evaluate educational strategies; the author takes on Eisner, Erickson, and Popkewitz.
Smith, J. (1997). The stories educational researchers tell about themselves. Educational Researcher, 33 (3), 4-11.
Recapitulates main features of an on-going debate between advocates for using vocabularies of traditional language arts and whole language in educational research. An "impasse" exists were advocates "do not share a theoretical disposition concerning both language instruction and the nature of research," Smith writes (p. 6). He includes a very comprehensive history of the debate of traditional research methodology and qualitative methods and vocabularies. Definitely worth a read by graduates.
Smith, N. L. (1980). The feasibility and desirability of experimental methods in evaluation. Evaluation and Program Planning: An International Journal , 251-55.
Smith identifies the conditions under which experimental research is most desirable. Includes a review of current thinking and controversies.
Stewart, N. R., & Johnson, R. G. (1986, March 16-20). An evaluation of experimental methodology in counseling and counselor education research. Paper presented at the annual meeting of the American Educational Research Association, San Francisco.
The purpose of this study was to evaluate the quality of experimental research in counseling and counselor education published from 1976 through 1984.
Spector, P. E. (1990). Research Designs. Newbury Park, California: Sage Publications.
In this book, Spector introduces the basic principles of experimental and nonexperimental design in the social sciences.
Tait, P. E. (1984). Do-it-yourself evaluation of experimental research. Journal of Visual Impairment and Blindness, 78 , 356-363 .
Tait's goal is to provide the reader who is unfamiliar with experimental research or statistics with the basic skills necessary for the evaluation of research studies.
Walsh, S. M. (1990). The current conflict between case study and experimental research: A breakthrough study derives benefits from both . (ERIC Document Number ED339721).
This paper describes a study that was not experimentally designed, but its major findings were generalizable to the overall population of writers in college freshman composition classes. The study was not a case study, but it provided insights into the attitudes and feelings of small clusters of student writers.
Waters, G. R. (1976). Experimental designs in communication research. Journal of Business Communication, 14 .
The paper presents a series of discussions on the general elements of experimental design and the scientific process and relates these elements to the field of communication.
Welch, W. W. (March 1969). The selection of a national random sample of teachers for experimental curriculum evaluation. Scholastic Science and Math , 210-216.
Members of the evaluation section of Harvard project physics describe what is said to be the first attempt to select a national random sample of teachers, and list 6 steps to do so. Cost and comparison with a volunteer group are also discussed.
Winer, B.J. (1971). Statistical principles in experimental design , (2nd ed.). New York: McGraw-Hill.
Combines theory and application discussions to give readers a better understanding of the logic behind statistical aspects of experimental design. Introduces the broad topic of design, then goes into considerable detail. Not for light reading. Bring your aspirin if you like statistics. Bring morphine is you're a humanist.
Winn, B. (1986, January 16-21). Emerging trends in educational technology research. Paper presented at the Annual Convention of the Association for Educational Communication Technology.
This examination of the topic of research in educational technology addresses four major areas: (1) why research is conducted in this area and the characteristics of that research; (2) the types of research questions that should or should not be addressed; (3) the most appropriate methodologies for finding answers to research questions; and (4) the characteristics of a research report that make it good and ultimately suitable for publication.
Luann Barnes, Jennifer Hauser, Luana Heikes, Anthony J. Hernandez, Paul Tim Richard, Katherine Ross, Guo Hua Yang, and Mike Palmquist. (1994-2024). Experimental and Quasi-Experimental Research. The WAC Clearinghouse. Colorado State University. Available at https://wac.colostate.edu/repository/writing/guides/.
Copyright © 1994-2024 Colorado State University and/or this site's authors, developers, and contributors . Some material displayed on this site is used with permission.
--> (2014) Doctoral Dissertation, University of Pittsburgh. (Unpublished) ) --> |
Over the past couple of decades, teacher effectiveness has become a major focus to improve students’ mathematics learning. Teacher professional development (PD), in particular, has been at the center of efforts aimed at improving teaching practice and the mathematics learning of students. However, empirical evidence for the effectiveness of PD for improving student achievement is mixed and there is limited research-based knowledge about the features of effective PD not only in mathematics but also in other subject areas. In this quasi-experimental study, I examined the effect of a Math and Science Partnership (MSP) PD on student achievement trajectories. Results of hierarchical growth models for this study revealed that content-focused (Algebra1 and Geometry), ongoing PD was effective for improving student achievement (relative to a matched comparison group) in Algebra1 (both for high and low performing students) and in Geometry (for low performing students only). There was no effect of PD on students’ achievement in Algebra2, which was not the focus of the MSP-PD. By demonstrating an effect of PD on student achievement, this study contributes to our growing knowledge base about features of PD programs that appear to contribute to their effectiveness. Moreover, it provides a case study showing how the research design might contribute in important ways to the ability to detect an effect of PD -if one exists- on student achievement. For example, given the data I had from the district, I was able to examine student growth within all Algebra 1, Geometry and Algebra 2 courses, while matching classrooms on aggregate student characteristics and school contexts. This allowed me to eliminate the potential confound of curriculum and to utilize longitudinal models to examine PD effects on students’ growth (relative to a comparison sample) for matched classrooms. Findings of this study have implications for educational practitioners and policymakers in their efforts to design and support effective PD programs in mathematics, and these features likely transfer to the design of PD in all subject areas. Moreover, for educational researchers this study suggests potential strategies for demonstrating robust research-based evidence for the effectiveness of PD on student learning.
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Revised on January 22, 2024. Like a true experiment, a quasi-experimental design aims to establish a cause-and-effect relationship between an independent and dependent variable. However, unlike a true experiment, a quasi-experiment does not rely on random assignment. Instead, subjects are assigned to groups based on non-random criteria.
Quasi-Experimental Design Examples. 1. Smartboard Apps and Math. A school has decided to supplement their math resources with smartboard applications. The math teachers research the apps available and then choose two apps for each grade level. Before deciding on which apps to purchase, the school contacts the seller and asks for permission to ...
Quasi-experimental research designs are a type of research design that is similar to experimental designs but doesn't give full control over the independent variable (s) like true experimental designs do. In a quasi-experimental design, the researcher changes or watches an independent variable, but the participants are not put into groups at ...
A significant advantage of quasi-experimental research over purely observational studies and correlational research is that it addresses the issue of directionality, determining which variable is the cause and which is the effect. In quasi-experiments, an intervention typically occurs during the investigation, and the researchers record outcomes before and after it, increasing the confidence ...
See why leading organizations rely on MasterClass for learning & development. A quasi-experimental design can be a great option when ethical or practical concerns make true experiments impossible, but the research methodology does have its drawbacks. Learn all the ins and outs of a quasi-experimental design.
Describe three different types of quasi-experimental research designs (nonequivalent groups, pretest-posttest, and interrupted time series) and identify examples of each one. The prefix quasi means "resembling.". Thus quasi-experimental research is research that resembles experimental research but is not true experimental research.
Quasi-experimental design is a research method that seeks to evaluate the causal relationships between variables, but without the full control over the independent variable (s) that is available in a true experimental design. In a quasi-experimental design, the researcher uses an existing group of participants that is not randomly assigned to ...
2. Quasi-experimental design. A quasi-experiment is a non-randomized study used to evaluate the effect of an intervention. So in a quasi-experiment, the decision of who gets to use the app and who doesn't is not made at random. Instead, participants will be assigned according to their choosing or that of the researcher.
A quasi-experimental study (also known as a non-randomized pre-post intervention) is a research design in which the independent variable is manipulated, but participants are not randomly assigned to conditions. Commonly used in medical informatics (a field that uses digital information to ensure better patient care), researchers generally use ...
In medical informatics, the quasi-experimental, sometimes called the pre-post intervention, design often is used to evaluate the benefits of specific interventions. The increasing capacity of health care institutions to collect routine clinical data has led to the growing use of quasi-experimental study designs in the field of medical ...
Quasi-Experimental Designs. By: John F. Stevenson | Edited by: Paul Atkinson, Sara ... Watch videos from a variety of sources bringing classroom topics to life. Read modern, diverse business cases. Explore hundreds of books and reference titles ... About Sage Publishing About Sage Research Methods Accessibility Author Guidelines AI/LLM CCPA ...
Quasi-experimental research designs are the most widely used research approach employed to evaluate the outcomes of social work programs and policies. This new volume describes the logic, design ...
Chapter 10 shows where the four prototypical quasi- experimental designs fall within the more general typology and notes how the logic of the design and the analysis of the four prototypical designs generalize to the other designs in the typology. Chapter 11 expands upon the typology presented in Chapter 10, showing how each fundamental design ...
In the past few decades, we have seen a rapid proliferation in the use of quasi-experimental research designs in education research. This trend, stemming in part from the "credibility revolution" in the social sciences, particularly economics, is notable along with the increasing use of randomized controlled trials in the strive toward rigorous causal inference.
An experimental design is a randomized study design used to evaluate the effect of an intervention. In its simplest form, the participants will be randomly divided into 2 groups: A treatment group: where participants receive the new intervention which effect we want to study. A control or comparison group: where participants do not receive any ...
The prefix quasi means "resembling." Thus quasi-experimental research is research that resembles experimental research but is not true experimental research. Although the independent variable is manipulated, participants are not randomly assigned to conditions or orders of conditions (Cook & Campbell, 1979). [1] Because the independent variable is manipulated before the dependent variable ...
QEDs test causal hypotheses but, in lieu of fully randomized assignment of the intervention, seek to define a comparison group or time period that reflects the counter-factual (i.e., outcomes if the intervention had not been implemented) ().QEDs seek to identify a comparison group or time period that is as similar as possible to the treatment group or time period in terms of baseline (pre ...
Experimental and Quasi-Experimental Research. Guide Title: Experimental and Quasi-Experimental Research Guide ID: 64. You approach a stainless-steel wall, separated vertically along its middle where two halves meet. After looking to the left, you see two buttons on the wall to the right. You press the top button and it lights up.
For example, in a quasi-experimental study, ... Psychology Cause & Effect Essay Topics; Descriptive Research Design: Definition, Example & Types; Psychology 311 - Assignment 1: Research Topic ...
Segmented Polynomial Models in Quasi-Experimental Research. ERIC Educational Resources Information Center. Wasik, John L. 1981-01-01. The use of segmented polynomial models is explained. Examples of design matrices of dummy variables are given for the least squares analyses of time series and discontinuity quasi-experimental research
Quasi-Experimental Designs Many types of Research designs beyond the scope of this course Right now, reading and understanding research is the goal To learn more, take more courses, get involved in research (DIS opportunities), read books and articles Psychology is a research-based discipline
experimental group participated in the performance assessment based teaching-learning activities for nine weeks. After nine weeks, three post-tests were administered to both the experimental group and control group (More details about the quasi-experimental research procedure may be found within the fourth portion of this section). Table 1.
In this quasi-experimental study, I examined the effect of a Math and Science Partnership (MSP) PD on student achievement trajectories. ... Moreover, it provides a case study showing how the research design might contribute in important ways to the ability to detect an effect of PD -if one exists- on student achievement. For example, given the ...
When considering internal data or the results of a study, often business leaders either take the evidence presented as gospel or dismiss it altogether. Both approaches are misguided. What leaders ...