实验设计理论：统计结构与关键概念

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"实验设计理论" 本书是对实验设计的主要议题的深入探讨，特别关注其中的关键概念及其相关的统计结构。尽管实验设计在统计学领域已经相当成熟，但在许多学习统计学的课程中，它往往不如分析方法那样受到重视。实验设计理论是统计学中的一个核心分支，它涉及到如何有效地组织和安排实验，以获取最有效的数据，从而能够更准确地推断出因果关系和变量间的相互作用。D.R.COX和N.REID两位作者，分别来自牛津大学的Nuffield学院和多伦多大学，以其深厚的学术背景和专业经验，对这一主题进行了详尽的阐述。书中的内容可能涵盖了以下关键知识点： 1. 实验设计的基本原则：包括随机化、区组化和重复原则，这些原则帮助消除潜在的偏倚，确保实验结果的可靠性。 2. 完全随机设计：这是一种常见的实验设计类型，其中每个处理都可能被随机分配到每个实验单元。这种设计简单且易于分析，但可能无法充分控制环境因素的影响。 3. 析因设计：允许同时研究多个因素及其交互效应的设计，有助于更全面地理解系统的复杂性。 4. 拉丁方设计和正交设计：这两种设计通过排列组合确保了所有可能的处理组合都被使用，减少了试验次数并提高了效率。 5. 区组设计：将实验单元分组，每组内部的变异较小，可减小环境影响，提高实验效果的比较性。 6. 响应曲面设计：用于优化多变量过程，通过多轮实验收集数据，构建响应曲面模型，找到最优操作条件。 7. 统计分析：包括方差分析、回归分析、假设检验等方法，用于分析实验数据，确定处理效应是否显著。 8. 最优设计：寻找能够最小化测量误差或最大化信息量的设计，例如D-optimal、A-optimal和E-optimal设计。 9. 混合模型：处理固定效应和随机效应的组合，适用于存在重复测量或嵌套结构的实验。 10. 实验设计的伦理与实践：包括如何保护实验对象、数据隐私以及实验的道德考量。书中引用了多种来源的信息，并提供了广泛的参考文献，尽管作者和出版商已尽力提供可靠的数据和信息，但他们并不对所有材料的准确性和使用后果负责。任何复制或传播本书内容的行为，都需要事先获得CRC Press LLC的书面许可。《实验设计理论》是一本深度剖析实验设计理论和实践的著作，对于从事科学研究、质量控制、生物医学研究等领域的人士来说，是一份宝贵的学习和参考资料。

jects, avoidance of bias, while still important, is not usually the

aspect of main concern.

These objectives have to be secured subject to the practical con-

straints of the situation under study. The designs and considera-

tions developed in this book have often to be adapted or modiﬁed

to meet such constraints.

1.5 Interplay between design and analysis

There is a close connection between design and analysis in that an

objective of design is to make both analysis and interpretation as

simple and clear as possible. Equally, while some defects in design

may be corrected by more elaborate analysis, there is nearly always

some loss of security in the interpretation, i.e. in the underlying

subject-matter meaning of the outcomes.

The choice of detailed model for analysis and interpretation will

often involve subject-matter considerations that cannot readily be

discussed in a general book such as this. Partly but not entirely

for this reason we concentrate here on the analysis of continuously

distributed responses via models that are usually linear, leading to

analyses quite closely connected with the least-squares analysis of

the normal theory linear model. One intention is to show that such

default analyses follow from a single set of assumptions common to

the majority of the designs we shall consider. In this rather special

sense, the model for analysis is determined by the design employed.

Of course we do not preclude the incorporation of special subject-

matter knowledge and models where appropriate and indeed this

may be essential for interpretation.

There is a wider issue involved especially when a number of dif-

ferent response variables are measured and underlying interpreta-

tion is the objective rather than the direct estimation of treatment

diﬀerences. It is sensible to try to imagine the main patterns of

response that are likely to arise and to consider whether the infor-

mation will have been collected to allow the interpretation of these.

This is a broader issue than that of reviewing the main scheme of

analysis to be used. Such consideration must always be desirable;

it is, however, considerably less than a prior commitment to a very

detailed approach to analysis.

Two terms quite widely used in discussions of the design of ex-

periments are balance and orthogonality. Their deﬁnition depends a

bit on context but broadly balance refers to some strong symmetry

in the combinatorial structure of the design, whereas orthogonal-

ity refers to special simpliﬁcations of analysis and achievement of

eﬃciency consequent on such balance.

For example, in Chapter 3 we deal with designs for a number of

treatments in which the experimental units are arranged in blocks.

The design is balanced if each treatment occurs in each block the

same number of times, typically once. If a treatment occurs once

in some blocks and twice or not at all in others the design is con-

sidered unbalanced. On the other hand, in the context of balanced

incomplete block designs studied in Section 4.2 the word balance

refers to an extended form of symmetry.

In analyses involving a linear model, and most of our discussion

centres on these, two types of eﬀect are orthogonal if the relevant

columns of the matrix deﬁning the linear model are orthogonal in

the usual algebraic sense. One consequence is that the least squares

estimates of one of the eﬀects are unchanged if the other type of

eﬀect is omitted from the model. For orthogonality some kinds of

balance are suﬃcient but not necessary. In general statistical theory

there is an extended notion of orthogonality based on the Fisher

information matrix and this is relevant when maximum likelihood

analysis of more complicated models is considered.

1.6 Key steps in design

1.6.1 General remarks

Clearly the single most important aspect of design is a purely sub-

stantive, i.e. subject-matter, one. The issues addressed should be

interesting and fruitful. Usually this means examining one or more

well formulated questions or research hypotheses, for example a

speculation about the process underlying some phenomenon, or

the clariﬁcation and explanation of earlier ﬁndings. Some investi-

gations may have a less focused objective. For example, the initial

phases of a study of an industrial process under production con-

ditions may have the objective of identifying which few of a large

number of potential inﬂuences are most important. The methods

of Section 5.6 are aimed at such situations, although they are prob-

ably atypical and in most cases the more speciﬁc the research ques-

tion the better.

In principle therefore the general objectives lead to the following

more speciﬁc issues. First the experimental units must be deﬁned

and chosen. Then the treatments must be clearly deﬁned. The vari-

ables to be measured on each unit must be speciﬁed and ﬁnally the

size of the experiment, in particular the number of experimental

units, has to be decided.

1.6.2 Experimental units

Issues concerning experimental units are to some extent very spe-

ciﬁc to each ﬁeld of application. Some points that arise fairly gen-

erally and which inﬂuence the discussion in this book include the

following.

Sometimes, especially in experiments with a technological focus,

it is useful to consider the population of ultimate interest and the

population of accessible individuals and to aim at conclusions that

will bridge the inevitable gap between these. This is linked to the

question of whether units should be chosen to be as uniform as

possible or to span a range of circumstances. Where the latter is

sensible it will be important to impose a clear structure on the

experimental units; this is connected with the issue of the choice

of baseline measurements.

Illustration. In agricultural experimentation with an immediate

objective of making recommendations to farmers it will be impor-

tant to experiment in a range of soil and weather conditions; a

very precise conclusion in one set of conditions may be of limited

value. Interpretation will be much simpliﬁed if the same basic de-

sign is used at each site. There are somewhat similar considerations

in some clinical trials, pointing to the desirability of multi-centre

trials even if a trial in one centre would in principle be possible.

By contrast in experiments aimed at elucidating the nature of

certain processes or mechanisms it will usually be best to choose

units likely to show the eﬀect in question in as striking a form as

possible and to aim for a high degree of uniformity across units.

In some contexts the same individual animal, person or material

may be used several times as an experimental unit; for example

in a psychological experiment it would be common to expose the

same subject to various conditions (treatments) in one session.

It is important in much of the following discussion and in ap-

plications to distinguish between experimental units and observa-

tions. The key notion is that diﬀerent experimental units must in

principle be capable of receiving diﬀerent treatments.

Illustration. In an industrial experiment on a batch process each

separate batch of material might form an experimental unit to be

processed in a uniform way, separate batches being processed pos-

sibly diﬀerently. On the product of each batch many samples may

be taken to measure, say purity of the product. The number of

observations of purity would then be many times the number of

experimental units. Variation between repeat observations within

a batch measures sampling variability and internal variability of

the process. Precision of the comparison of treatments is, how-

ever, largely determined by, and must be estimated from, variation

between batches receiving the same treatment. In our theoretical

treatment that follows the number of batches is thus the relevant

total “sample” size.

1.6.3 Treatments

The simplest form of experiment compares a new treatment or

manipulation, T , with a control, C. Even here care is needed in

applications. In principle T has to be speciﬁed with considerable

precision, including many details of its mode of implementation.

The choice of control, C, may also be critical. In some contexts

several diﬀerent control treatments may be desirable. Ideally the

control should be such as to isolate precisely that aspect of T which

it is the objective to examine.

Illustration. In a clinical trial to assess a new drug, the choice of

control may depend heavily on the context. Possible choices of con-

trol might be no treatment, a placebo treatment, i.e. a substance

superﬁcially indistinguishable from T but known to be pharma-

cologically inactive, or the best currently available therapy. The

choice between placebo and best available treatment may in some

clinical trials involve diﬃcult ethical decisions.

In more complex situations there may be a collection of quali-

tatively diﬀerent treatments T

,...,T

. More commonly the treat-

ments may have factorial structure, i.e. be formed from combina-

tions of levels of subtreatments, called factors. We defer detailed

study of the diﬀerent kinds of factor and the design of factorial

experiments until Chapter 5, noting that sensible use of the prin-

ciple of examining several factors together in one study is one of

the most powerful ideas in this subject.

1.6.4 Measurements

The choice of appropriate variables for measurement is a key aspect

of design in the broad sense. The nature of measurement processes

and their associated potentiality for error, and the diﬀerent kinds

of variable that can be measured and their purposes are central is-

sues. Nevertheless these issues fall outside the scope of the present

book and we merely note three broad types of variable, namely

baseline variables describing the experimental units before appli-

cation of treatments, intermediate variables and response variables,

in a medical context often called end-points.

Intermediate variables may serve diﬀerent roles. Usually the more

important is to provide some provisional explanation of the process

that leads from treatment to response. Other roles are to check on

the absence of untoward interventions and, sometimes, to serve as

surrogate response variables when the primary response takes a

long time to obtain.

Sometimes the response on an experimental unit is in eﬀect a

time trace, for example of the concentrations of one or more sub-

stances as transient functions of time after some intervention. For

our purposes we suppose such responses replaced by one or more

summary measures, such as the peak response or the area under

the response-time curve.

Clear decisions about the variables to be measured, especially

the response variables, are crucial.

1.6.5 Size of experiment

Some consideration virtually always has to be given to the num-

ber of experimental units to be used and, where subsampling of

units is employed, to the number of repeat observations per unit.

A balance has to be struck between the marginal cost per exper-

imental unit and the increase in precision achieved per additional

unit. Except in rare instances where these costs can both be quan-

tiﬁed, a decision on the size of experiment is bound be largely a

matter of judgement and some of the more formal approaches to

determining the size of the experiment have spurious precision. It

is, however, very desirable to make an advance approximate cal-

culation of the precision likely to be achieved. This gives some

protection against wasting resources on unnecessary precision or,

more commonly, against undertaking investigations which will be

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